Artificial intelligence in oncology: linking biological discovery to clinical utility

Abstract

Background

Artificial intelligence (AI) has expanded rapidly across the oncology continuum—spanning early detection, histopathology, molecular profiling, treatment selection, drug discovery, toxicity surveillance, and survivorship care. However, these varied applications occupy fundamentally different stages of clinical and biological translation.

Methods

We conducted a critical narrative review searching PubMed/MEDLINE, Europe PMC, IEEE Xplore, arXiv, and ClinicalTrials.gov (updated to July 21, 2026). From these sources, an evidence map of 202 publications (including 182 original studies) was assembled based on study design, prospective or external validation, mechanistic rigor, clinical utility, and representation across the cancer continuum.

Results

The primary synthesis demonstrates evidence gradient rather than uniform translation across oncology: Detection & Imaging: Select mammography and colonoscopy tools are supported by randomized controlled trials demonstrating workflow efficiency and detection gains. Conversely, negative pragmatic trials highlight that robust technical accuracy does not automatically translate into improved diagnostic pathways. Pathology: Large self-supervised and vision–language foundational models exhibit strong cross-task and cross-institutional transferability. However, prospective real-world deployment remains rare, and reporting on calibration, subgroup performance, and data provenance is inconsistent. Molecular & Systems Biology: Multi-omics, single-cell, spatial transcriptomics, graph-based, and perturbation models increasingly yield falsifiable hypotheses regarding tumor microenvironments, regulatory networks, and drug vulnerabilities; most, however, lack upstream functional validation. Therapeutic Decision Support: Applications in treatment response, surgical assistance, toxicity monitoring, and clinical large language models (LLMs) remain limited by cohort heterogeneity, temporal drift, unstandardized endpoints, and a lack of evidence that model-guided care alters patient outcomes.

Conclusion

AI applications must be evaluated using evidence matched directly to their specific clinical or biological claims: external validation for transportability, calibration/decision analysis for utility, prospective workflow studies for operational value, randomized trials for patient outcome benefits, and perturbation experiments for biological mechanism. This claim-matched framework clarifies the boundary between promising computational models and clinically or mechanistically credible oncology, establishing a roadmap for reliable integration into precision cancer care.

Supplementary Information

The online version contains supplementary material available at https://doi.org/10.1186/s12943-026-02771-x.

Introduction

Cancer remains a leading cause of death worldwide, but its clinical burden cannot be reduced to incidence and mortality alone. Malignant disease is an evolving system in which spatially segregated subclones, immune and stromal compartments, treatment pressure, and host factors generate variation within one lesion, between lesions, and over time [1, 2]. Precision oncology consequently depends on linking observations made at different scales—from radiographic phenotype and tissue architecture to cell state, regulatory circuitry, and longitudinal clinical outcome—without mistaking correlation for mechanism or prediction for benefit [3, 4].

This is the setting in which AI has become consequential. Modern models can learn representations from mammograms, computed tomography, whole-slide images, bulk and single-cell omics, spatial assays, electronic records, and combinations of these data. They can estimate future cancer risk, infer molecular alterations from morphology, model cellular perturbations, and prioritize candidate therapies [5–8]. The scientific opportunity is substantial: AI can compress high-dimensional observations into clinically useful decisions or experimentally tractable hypotheses. The epistemic risk is equally substantial: the same flexibility allows models to exploit scanner signatures, institutional workflow, ancestry-linked proxies, label noise, and treatment-era effects.

The decisive question is therefore not whether AI can achieve a high area under the receiver-operating-characteristic curve (AUROC), but what claim the evidence permits. A retrospective test set can establish discrimination under sampled conditions; it cannot establish calibration in a new population, benefit at a clinical threshold, resilience after workflow integration, or improved patient outcome. Randomized mammography and colonoscopy studies have shown that AI can alter detection and workload, whereas pragmatic negative trials demonstrate that an apparently capable model may add little when baseline performance is high or when the targeted step is not the pathway bottleneck [9–12].

An analogous distinction is required for biological insight. A saliency map is not a mechanism, an association with response is not a predictive biomarker, and an in-silico perturbation is not synthetic lethality. Mechanistic credibility increases when a model identifies a reproducible biological construct, predicts an unseen perturbation, and survives orthogonal or functional validation. Clinical credibility increases through external validation, calibration, prospective workflow testing, and, when treatment is changed, randomized evaluation. This review integrates these two axes. It examines AI from molecular discovery to implementation, with particular emphasis on why some applications have crossed into prospective care while others remain biologically interesting but clinically unproven [13–15].

Methods

Review design and reporting approach

We conducted a critical narrative review because AI in oncology encompasses diagnostic-accuracy studies, prediction models, representation learning, perturbation experiments, clinical trials, and regulatory records that address different questions and cannot be combined into a single defensible estimand. The review was designed to compare evidence across four axes: the intended clinical or biological task, validation design, mechanistic content, and translational maturity. It was not registered as a systematic review, and no claim of exhaustive study capture or pooled effect estimation is made.

Information sources and search date

Structured PubMed/MEDLINE searches covered English-language publications from 1 January 2018 to 21 July 2026, including newly indexed prospective, foundation-model, multimodal, molecular-oncology, biomarker, and LLM studies. Europe PMC, the IEEE Xplore public search interface, arXiv, and ClinicalTrials.gov. Europe PMC was used both to retrieve peer-reviewed biomedical records and to identify articles outside the capped PubMed exports. IEEE Xplore was searched for journal, early-access, and conference records in multimodal learning, foundation models, graph learning, biological networks, and biomarker discovery. arXiv was searched to locate influential methods and their peer-reviewed versions; preprint-only reports were not used to support clinical claims. ClinicalTrials.gov and the US Food and Drug Administration (FDA) databases were used to verify trial and authorization status, and registry records were not counted as peer-reviewed original studies. Crossref and primary publisher records were used to confirm bibliographic identity, article type, digital object identifiers, and quantitative findings. Backward and forward citation tracking identified pre-2018 landmarks. Embase, Scopus, and Web of Science were not available and were not searched; this limitation informed the decision to present the work as a narrative rather than a systematic review.

Nine PubMed search blocks covered: (1) screening, imaging, and risk prediction; (2) digital and computational pathology; (3) multimodal learning, multi-omics, and biomarker discovery; (4) single-cell, spatial, perturbational, and network biology; (5) treatment-response prediction and drug discovery; (6) radiotherapy and surgical oncology; (7) large language models (LLMs) and clinical natural-language processing; (8) toxicity, symptom monitoring, and survivorship; and (9) external validation, prospective evaluation, and implementation. The supplementary databases used a broad oncology-AI query and narrower blocks for clinical translation, molecular and foundation models, biomarker discovery, and care-continuum applications. Exact strings, platform-specific filters, yields, retrieval rules, and selection outcomes are reported in Supplementary Appendix 1. Also, further analysis of the selected publications is shown in Supplementary Figs. 1–5.

Eligibility and evidence prioritization

Eligible evidence comprised peer-reviewed original studies applying machine learning, deep learning, radiomics, natural-language processing, graph learning, generative modelling, or foundation models to cancer biology, prevention, diagnosis, prognosis, treatment, supportive care, or implementation. A restricted set of reporting standards, empirical methodological studies, regulatory records, and trial registrations was retained when necessary to interpret claims of performance, clinical readiness, or current status. Narrative reviews, non-peer-reviewed summaries, conference-only records when a full article existed, and superseded preprints were excluded.

Evidence was prioritized in three tiers. The first comprised randomized trials, prospective studies, external or multinational validation, and real-world deployment. The second comprised original methods with broad methodological influence or direct capacity to generate testable biological hypotheses. The third comprised representative primary studies required to cover cancer types, modalities, or care stages not captured by the first two tiers. Journal prestige and citation visibility informed landmark recognition but never replaced assessment of design, endpoint, and claim–evidence fit. No standalone arXiv preprint, conference-only IEEE record, or registry-only ClinicalTrials.gov record was added as an original study. The resulting evidence map contained 202 sources, of which 182 were original studies, and 20 were methodological, reporting, regulatory, or registry sources.

Data extraction and critical appraisal

For each original study, we recorded bibliographic identifiers, cancer context, data modality, model family, cohort or corpus scale when reported, retrospective or prospective design, internal and external validation, multicentre status, endpoint, principal result, and major translational limitation. Numerical findings used in the text and tables were checked against the primary article or an official registry or regulatory record. We did not infer missing sample sizes or validation characteristics. Study identification and extraction were performed by the first author; the corresponding author reviewed the scientific synthesis and clinical interpretation. Independent duplicate screening and extraction were not undertaken.

Critical appraisal was adapted to study type. Prediction-model studies were examined for participant and data-source selection, outcome definition, overfitting, validation, calibration, subgroup analysis, and applicability, consistent with TRIPOD + AI and PROBAST + AI principles [16, 17]. Imaging studies were additionally assessed against CLAIM 2024 concepts, including data partitioning, reference standards, external testing, and failure analysis [18]. Early clinical evaluations were interpreted in relation to DECIDE-AI, and AI-intervention trials in relation to CONSORT-AI [19, 20]. Formal pooled risk-of-bias scoring was not attempted because the evidence included diagnostic studies, prediction models, randomized trials, preclinical molecular benchmarks, and regulatory records that cannot be evaluated validly with a single instrument.

Synthesis framework

Evidence was synthesized by question rather than chronology: whether validation was internal or external; whether evaluation was retrospective, prospective, or randomized; whether the endpoint represented discrimination, calibration, workflow change, clinical utility, or patient benefit; and whether a biological claim represented association, interpretable structure, perturbation prediction, orthogonal confirmation, or functional mechanism. Translational maturity was interpreted as a sequence from computational feasibility through external validation, prospective workflow evaluation, randomized impact evaluation, and monitored deployment (Supplementary Figs. 1–5).

Results

Evidence landscape

The evidence map contained 182 original studies across discovery, diagnosis, treatment, and longitudinal care. Imaging studies ranged from retrospective reader comparisons to multicentre validation, risk prediction, and randomized workflow trials [5, 9–12, 21–40]. Pathology progressed from weak supervision and molecular-surrogate prediction to multinational challenges, foundation models, and prospective silent deployment [41–61]. Multimodal and multi-omics studies combined clinical, imaging, histological, transcriptomic, proteomic, and genomic information, but most remained retrospective [4, 6, 8, 13, 14, 62–94]. Single-cell, spatial, structural, and network models provided the clearest route from representation learning to experimentally testable hypotheses [2, 7, 95–121].

The clinical evidence was more uneven. Radiotherapy studies included external commissioning, reader-workflow experiments, plan selection, and limited prospective deployment [122–136]; surgical studies concentrated on intraoperative recognition, image guidance, and margin assessment [3, 137–145]. Toxicity and survivorship evidence juxtaposed small predictive cohorts with large, randomized trials of non-AI digital symptom monitoring [146–156]. LLM studies moved rapidly from benchmark questions to report communication, trial matching, tumor-board concordance, and retrieval-grounded support [157–178]. Drug-response and discovery studies spanned cell-line benchmarks, trial-cohort biomarkers, generative chemistry, and first-in-human programmes [179–184]. Cross-cutting implementation studies addressed validation, automation, and model-supported clinical operations [185–189]. Because study selection was purposive, these distributions describe the architecture of the evidence, not field-wide prevalence.

A consistent maturity gradient emerged. Image-based applications benefit from abundant digitised inputs, comparatively observable labels, and workflows that can accommodate triage or a second reader. Treatment-response, multi-omics, and toxicity models face delayed and treatment-dependent outcomes, informative missingness, smaller cohorts, and rapidly changing standards of care. Foundation models can be pretrained at unprecedented scale, but scale is an upstream property: it does not substitute for external calibration, prospective impact evaluation, or experimental confirmation of mechanisms.

The coded corpus demonstrates that volume and maturity can diverge. Digital pathology had the largest evidence portfolio, whereas screening, supportive care, and selected workflow domains contributed a greater proportion of randomised evaluations. Molecular foundation-model and drug-discovery studies remain concentrated in internal, retrospective, or external benchmark evaluation. These patterns describe the selected evidence map rather than the publication landscape as a whole.

Cancer screening, early detection, and risk prediction

Mammography provides the clearest transition from retrospective comparison to randomized evaluation. McKinney and colleagues reported fewer false-positive and false-negative results in UK and US datasets and favourable performance against six radiologists, but constrained reader conditions and limited access to code and data prompted a consequential reproducibility debate [15, 24]. Independent commercial-algorithm evaluations subsequently showed clinically material variation between systems and populations, while annotation-efficient models and combined radiologist–AI assessment demonstrated that operating mode matters as much as stand-alone discrimination [23, 27, 47]. Mirai shifted the endpoint from current-cancer detection to 1–5-year risk, outperforming Tyrer–Cuzick in the MGH cohort and transferring to Swedish and Taiwanese cohorts; its single-vendor development nevertheless leaves calibration, image-acquisition shift, and downstream prevention thresholds as implementation questions [5].

The evidentiary standard is now higher. The MASAI randomized program found that AI-supported reading reduced workload and, in the completed population analysis, achieved non-inferior interval-cancer rates, higher sensitivity, and similar specificity compared with standard double reading [9, 29]. A 2026 multicenter technical-feasibility evaluation of a different mammography system found higher retrospective sensitivity and potential time savings but also identified prospective distribution shift requiring threshold recalibration [38]. Thus, even favorable deployment evidence supports monitored adaptation rather than static transport of a threshold between sites (Table 1).

Table 1.

Representative clinical and translational evaluations of artificial intelligence in oncology

Study	Cancer/task and scale	Design/validation	Principal finding	Critical interpretation
MASAI [9]	Mammography; >100,000 screened women	Population-based randomized non-inferiority study	Higher sensitivity, similar specificity, non-inferior interval-cancer rate, reduced reading burden	Strong screening evidence; generalizability depends on program design and vendor/workflow
LungIMPACT [12]	Lung diagnostic pathway; 93,326 analyzed chest X-rays (97,731 performed), five NHS trusts; 558 cancers	Multicenter randomized trial	No improvement in time to CT, diagnosis, treatment, or stage	Demonstrates pathway bottleneck and endpoint mismatch despite technical detection capability
Wang et al. [10]	Colonoscopy; 1,058 participants	Prospective randomized trial	Increased polyp and adenoma detection	Benefit established in controlled setting; effect depends on examiner and population
Zimmermann et al. [11]	Colonoscopy; 1,627 participants across 12 institutions	Pragmatic multicenter randomized study	No significant ADR improvement	Negative external context; examiner baseline performance modified value
Gao et al. [28]	Ovarian ultrasound; development in 105,532 patients and 2,092 validation patients	Retrospective ten-hospital study with two external cohorts and reader comparison	External AUROCs 0.870 and 0.831; AI assistance improved six radiologists’ average accuracy	Broad multicentre validation, but retrospective case construction does not establish screening-pathway benefit
Li et al. [32]	Oesophageal high-risk lesions; 3,117 patients	Prospective randomized controlled study	Detection increased from 0.9% to 1.8% (p = 0.029)	Positive clinical-impact evidence from one centre; low event counts and geographic transportability remain relevant
Yuan et al. [33]	Oesophageal lesions; 11,715 analysed patients across 12 hospitals	Multicentre tandem double-blind randomized trial	Numerically lower miss rates with AI, but confidence intervals crossed the null	Directionally favourable estimates are not definitive benefit; effectiveness and cost-benefit remain uncertain
Kickingereder et al. [179]	Neuro-oncology; 455 training patients and 2,034 scans from 532 EORTC-26,101 patients	Retrospective development with multicentre longitudinal trial-cohort validation	Automated volumetric time to progression was more reliable and more strongly associated with survival than RANO assessment	Improves quantitative endpoint reproducibility; prospective evidence that model use improves management is absent
McKinney et al. [24]	UK/US mammography and six-reader study	Retrospective international evaluation	Reduced false positives and false negatives in curated datasets	Reader conditions and reproducibility limitations constrain parity claims
Mirai [5]	1–5-year breast-cancer risk	Development plus international external cohorts	Outperformed Tyrer–Cuzick and transferred across cohorts	Development used one vendor; calibration and implementation require local evaluation
PANDA [51]	10,616 prostate biopsies; 1,290 developers	Blinded cross-continental challenge	Pathologist-level Gleason agreement	Strong reproducibility design, but distribution-shift overgrading persisted
EAGLE EGFR biomarker [86]	8,461 lung-adenocarcinoma slides; 197-sample silent cohort	Five-institution development/external testing plus prospective silent deployment	External AUROC 0.870; silent-cohort AUROC 0.890; simulated rapid-test reduction	Prospective transportability shown; clinical decisions and patient outcomes were not altered
Head-and-neck auto-contouring [128]	42 OARs; randomized reader workflow	Single-institution retrospective training and blinded workflow test	Reduced contouring and revision time	Clinically relevant workflow endpoint; external commissioning remains necessary
Prostate planning [187]	Curative prostate radiotherapy	Prospective blinded deployment	Most plans acceptable; planning time reduced	Planning choice is stronger than geometric similarity, but patient outcomes were not tested
Intraoperative brain diagnosis [137]	278 patients; stimulated Raman histology	Multicentre prospective non-inferiority study	Diagnosis in < 150 s; accuracy 94.6% versus 93.9% for conventional histology interpretation	Strong diagnostic-workflow evidence; effect on resection quality or outcomes was not tested
ICI ePRO toxicity model [147]	34 patients; 820 questionnaires	Exploratory model development	High AUROC but sparse positive events	High risk of optimism and leakage; not evidence of improved toxicity outcomes

Summary of pivotal clinical and translational studies evaluating Artificial Intelligence (AI) applications across screening, diagnostics, biomarker prediction, radiotherapy planning, and toxicity monitoring. Studies are categorized by target cancer/task, scale, validation design (ranging from retrospective multicenter cohorts to prospective randomized controlled trials), principal findings, and critical methodological or translational interpretations

Abbreviations: ADR Adenoma detection rate, AI Artificial intelligence, AUROC Area under the receiver-operating-characteristic curve, CT Computed tomography, EGFR Epidermal growth factor receptor, ePRO Electronic patient-reported outcome, irAE Immune-related adverse event, NHS National Health Service, OAR Organ at risk, EORTC European Organisation for Research and Treatment of Cancer, ICI Immune checkpoint inhibitor, RANO Response Assessment in Neuro-Oncology

Colorectal CADe studies illustrate both efficacy and contextual dependence. Early randomized trials increased adenoma detection [10, 46]. Two more recent pragmatic trials were negative. In CADLY2, AI assistance did not significantly improve adenoma detection during expert Lynch-syndrome surveillance (33.8% versus 30.9%; odds ratio 1.14, 95% CI 0.83–1.57), and a separate 1,627-patient, 12-institution trial likewise found no significant improvement, with examiner effects comparable to or larger than the intervention [11, 36]. Together, these trials suggest that baseline examiner performance, lesion prevalence, workflow, and surveillance setting modify incremental benefit. “CADe works” is therefore less informative than identifying where, for whom, and under which baseline conditions it adds net value.

Lung-cancer AI similarly separates prediction from pathway effect. Ardila and colleagues developed end-to-end three-dimensional CT screening, and Sybil predicted future lung-cancer risk from a single low-dose CT across independent cohorts [22, 31]. In LungIMPACT, 97,731 primary-care chest X-rays were performed and 93,326 were included in the multicenter randomized analysis across five NHS trusts; 558 lung cancers were identified. AI worklist prioritization did not shorten time to CT, diagnosis, referral, treatment, or stage at diagnosis, despite substantial discordance between AI and radiology reports [12]. This negative trial is translationally important: a technically capable model can fail when the intervention targets the wrong bottleneck in a multi-step clinical pathway.

Other screening studies broaden cancer representation but also expose the fragility of reference standards. In the Guanacaste cohort, automated visual evaluation of archived cervigrams yielded an AUROC of 0.91 for cumulative cervical precancer or cancer, compared with 0.69 for original cervigram interpretation and 0.71 for cytology; the retrospective image source and within-cohort validation limit direct inference to contemporary smartphone screening [21]. A 2026 randomized crossover study moved AI assistance into routine cervical cytopathology [59]. Prospective studies in endoscopic ultrasonography and low-prevalence pancreatic-cancer detection similarly emphasize rare-event performance and temporal stability [40, 60]. In these settings, sensitivity without calibrated positive predictive value and downstream-workup analysis can create diagnostic burden rather than benefit.

Evidence in ovarian and oesophageal cancer further illustrates why multicentre validation and randomised impact evaluation answer different questions. A pelvic-ultrasound model trained across ten Chinese hospitals achieved AUROCs of 0.870 and 0.831 in two external cohorts and improved six radiologists’ average accuracy, but the retrospective design does not establish effect in a screening pathway [28]. In a 3,117-patient randomised study, AI-assisted endoscopy doubled detection of high-risk oesophageal lesions from 0.9% to 1.8% (p = 0.029) [32]. By contrast, a 12-hospital tandem trial involving 11,715 analysed patients produced numerically lower per-lesion and per-patient miss rates with AI, but both confidence intervals crossed the null [33]. The comparison cautions against treating directionally favourable point estimates as established benefit when event counts are low and uncertainty remains wide.

Selected controlled evaluations reinforce why clinical effect must be interpreted by endpoint and setting. Detection improved in one colonoscopy trial and in routine cervical cytopathology, but confidence intervals crossed the null for CADLY2, MASAI interval cancer, LungIMPACT pathway times, and AI-triggered trial enrolment; PRO-TECT is included only as a non-AI digital-monitoring benchmark [9, 12, 36, 46, 59, 83, 151]. The heterogeneity of interventions, effect measures, and clinical targets precludes a pooled estimate and makes selective reporting of favourable endpoints particularly misleading.

Digital pathology: from task-specific classifiers to foundation models

Weak supervision was a decisive enabling step. Campanella and colleagues trained on 44,732 whole-slide images from 15,187 patients using slide-level labels and achieved high discrimination for prostate cancer, basal-cell carcinoma, and nodal metastases [42]. Data-efficient multiple-instance learning reduced annotation requirements further [48]. These methods solved an important scaling problem, but slide-level labels can preserve institutional and preparation artifacts that models exploit as shortcuts.

The strongest validation designs deliberately address that concern. The PANDA challenge included 10,616 prostate biopsies, 1,290 developers, and blinded cross-continental cohorts; leading algorithms achieved pathologist-level Gleason agreement, while localized overdiagnosis under distribution shift exposed residual fragility [51]. CAMELYON demonstrated competitive nodal-metastasis detection under controlled conditions, and AI-assisted prostate-pathology studies showed that augmentation can increase sensitivity without necessarily sacrificing specificity [41, 52]. These results support triage and second-reader use more strongly than autonomous diagnosis.

Histology can also act as a molecular surrogate. Coudray and colleagues predicted NSCLC subtype and recurrent alterations including STK11, EGFR, and TP53 from hematoxylin-and-eosin images [6]. MSI prediction has been replicated across gastrointestinal cancers, and pan-cancer studies have inferred actionable alterations, RNA expression, tumor composition, and prognosis [43, 68, 69, 72, 73]. The clinical risk is asymmetric: a morphology-based biomarker may efficiently rule in confirmatory testing or preserve tissue, but replacing molecular testing requires very high, externally calibrated negative predictive performance across demographic, scanner, and preparation strata.

Foundation models increase breadth but do not remove this requirement. UNI was pretrained on more than 100 million patches from more than 100,000 whole-slide images and evaluated across 34 tasks; CONCH linked pathology images with language; Virchow used approximately 1.5 million slides with emphasis on rare cancers; Prov-GigaPath used 1.3 billion tiles from 171,189 slides; and CHIEF combined tile- and slide-level pretraining across 60,530 slides and validated on 19,491 slides from independent cohorts [53–55, 78, 79] (Table 2). PathChat added a conversational multimodal interface, and newer vision–language and whole-slide models extended pretraining toward cross-modal retrieval, diagnosis, and precision-oncology tasks [56, 82, 161].

Table 2.

Representative foundation and mechanism-oriented models in oncology

Model/study	Training or evaluation scale	Biological output	Validation level	Main limitation
UNI [55]	> 100 million patches; >100,000 slides	Transferable pathology representations	34 downstream tasks	Benchmark transfer is not prospective utility
CONCH [53]	Large image–text pathology corpus	Zero/few-shot classification and retrieval	Multi-task benchmark	Language alignment can inherit label and text biases
Virchow [78]	~ 1.5 million slides	Common and rare cancer representation	Multicohort evaluation	Rare-cancer calibration and prospective error monitoring remain limited
Prov-GigaPath [54]	1.3 billion tiles; 171,189 slides	Whole-slide contextual representation	Multiple downstream tasks	Health-network provenance may encode site-specific practice
CHIEF [79]	60,530 development and 19,491 validation slides	Detection, origin, molecular and prognostic prediction	32 independent slide sets	Heterogeneous tasks complicate a single claim of clinical grade
HEX [90]	819,000 image tiles from 382 tumours; six independent NSCLC cohorts comprising 2,298 patients	Predicted expression of 40 proteins and interpretable spatial tumour–immune niches	Matched spatial-proteomic development data plus independent clinical cohorts	Virtual protein maps remain predictions; causal and treatment-selection claims require orthogonal and functional validation
GBCseeker [85]	301 prospectively enrolled patients from 11 centres	Integrated cfDNA, radiomics, and clinical variables for gallbladder-cancer diagnosis	Prospective multicentre study with independent external cohort	Modest sample size, one-country setting, and no randomized test of downstream surgical benefit
Geneformer [112]	Tens of millions of cells	Network hierarchy and in-silico perturbation	Experimental case studies	Perturbation predictions remain context-dependent hypotheses
scGPT [7]	> 33 million cells	Annotation, integration, perturbation and gene-network inference	Multi-task benchmark	Benchmark leakage and biological plausibility require scrutiny
scFoundation [114]	> 50 million cells	Expression enhancement, drug response, gene modules	Multi-task benchmark	Limited prospective or functional validation
GEARS [115]	Perturb-seq benchmarks	Unseen multigene perturbation response	Held-out perturbations	Transcriptomic prediction does not establish phenotype or synthetic lethality
Mo et al. [2]	131 spatial sections from 78 cases plus matched modalities	Spatial subclones and boundary interactions	Multicancer atlas with orthogonal data	Discovery cohort; candidate mechanisms require perturbation
MOGONET [74]	Multiple cancer multi-omics cohorts	Cross-omic graph features and biomarkers	Benchmark cohorts	Biomarker stability and causal relevance uncertain
COMPASS [93]	10,184 tumors; 16 clinical cohorts	Interpretable immune concepts and response hypotheses	Cross-cancer external cohorts	Prospective treatment-assignment utility not established
PathPrism [61]	7,000 colorectal-cancer patients; 11 cohorts	Spatial semantics linked to prognosis, molecular alterations, and chemotherapy benefit	Retrospective multicohort validation	Virtual perturbation is hypothesis generation, not functional validation
CHROMA [87]	~ 4 million chromosome images; 84,471 specimens	Numerical and structural cytogenetic abnormality representations with risk-controlled abstention	Held-out downstream tasks	Predominantly single-institution pretraining and internal validation

Overview of key foundation models, spatial multimodal frameworks, multi-omic graph architectures, and single-cell/cytogenetic transformers operating across pathology, transcriptomics, genomics, and cytogenetics. Models are summarized by their training or evaluation scale (e.g., slide volume, cell counts, chromosome image volume, multi-center patient cohorts), target biological output, validation depth across downstream tasks or independent external series, and primary methodological or translational limitations

Abbreviations: AI Artificial intelligence, CHIEF Clinical Histopathology Imaging Evaluation Foundation, CONCH Contrastive learning from Captions for Histopathology, GEARS Graph-enhanced gene activation and repression simulator, cfDNA Cell-free DNA, NSCLC Non-small cell lung cancer. Approximate values are identified with a tilde; greater-than signs indicate lower-bound corpus sizes reported by the source study

The critical question has shifted from whether representations transfer to whether they improve decisions. EAGLE was developed and tested in an international dataset of 8,461 lung-adenocarcinoma slides; external AUROC was 0.870 and a 197-sample prospective silent cohort yielded an AUROC of 0.890 (Table 1). The proposed workflow could reduce rapid EGFR testing while retaining confirmatory sequencing, but the silent design did not measure treatment or patient outcomes [86]. Conversely, demographic audits show that self-supervised representations may reduce but do not eliminate subgroup error differences [14]. Foundation-model reports should therefore pair scale with provenance, institution count, scanner and stain diversity, subgroup composition, calibration, abstention behaviour, and prospective error monitoring.

Multimodal learning and AI-generated biological insight

Multimodal models seek information that no single modality contains. Pathomic Fusion, pan-cancer histology–genomic integration, and multimodal survival models combine morphology with molecular profiles to improve risk stratification [4, 8, 26, 66]. MOGONET represents each omics layer as a graph and integrates cross-omic evidence for classification and biomarker identification [74] (Table 2). In breast cancer, a multi-omic machine-learning model predicted neoadjuvant response using clinical, imaging, digital-pathology, genomic, and transcriptomic information, illustrating the benefit of aligning data around a clinically meaningful endpoint [3].

Two recent studies sharpen the distinction between multimodal prediction and interpretable biomarker discovery. GBCseeker combined cell-free-DNA signatures, radiomics, and clinical variables in 301 prospectively enrolled patients from 11 centres, achieving 87.76% accuracy in an independent external cohort and reducing surgeons’ diagnostic errors by 56.24%; its size, geographic concentration, and decision-specific workflow still require broader impact evaluation [85]. HEX was trained on 819,000 image tiles with matched expression of 40 proteins from 382 tumours and evaluated across six independent non-small-cell lung-cancer cohorts comprising 2,298 patients (Table 2). Combining routine histology with virtual spatial proteomics improved reported prognostic accuracy by 22% and immunotherapy-response prediction by 24–39%, while identifying response-associated tumour–immune neighbourhoods [90]. These are biologically interpretable hypotheses derived from predicted—not directly measured—protein maps; orthogonal spatial-proteomic and perturbational validation remains necessary before causal or treatment-selection claims are warranted.

Yet multimodal gain is not synonymous with biological discovery. Fusion may improve prediction because modalities encode correlated proxies without identifying the causal process. Evidence is stronger when a model exposes a stable biological construct, predicts an unseen perturbation, or yields a hypothesis that can be tested independently. A 2026 pan-cancer transcriptomic foundation model represented immune states and tumour–microenvironment processes through biologically grounded concepts and generalized immunotherapy-response prediction across clinical cohorts; the implicated TGF-β, endothelial-exclusion, T-cell-dysfunction, and B-cell programmes remain hypotheses pending functional validation [93]. CHROMA illustrates a complementary task: self-supervised pretraining on approximately 4 million chromosome images enabled risk-controlled detection of numerical and structural abnormalities, but most pretraining data came from one institution and downstream testing remained internal [87] (Table 2).

Single-cell models move closer to mechanism by modeling cellular state and response. scVI and totalVI established deep generative integration of transcriptomic and multi-omic single-cell data [95, 103]. Geneformer learned network representations from tens of millions of cells and used in-silico perturbation to prioritize network effects; scGPT, scFoundation, and scBERT extended foundation pretraining to annotation, integration, gene-network inference, and perturbation tasks [7, 112, 114, 158]. scGen, compositional perturbation autoencoders, and GEARS directly model transcriptional responses to unseen or combinatorial perturbations [96, 110, 115].

Spatial models restore tissue context lost during dissociation. Tangram aligns single-cell profiles to spatial measurements; cell2location maps fine-grained cell types; and SpaGCN, STAGATE, and GraphST use spatial graphs to define domains, integrate samples, and deconvolve cell populations [75, 100, 107, 108, 111]. In cancer, multimodal atlases have identified microregional evolutionary structure and tumour–microenvironment boundaries, whereas virtual spatial profiling models infer cellular neighbourhoods or transcriptional programmes from routine histology [2, 116, 117]. PathPrism encoded interpretable spatial features in 7,000 patients with colorectal cancer across 11 cohorts and associated them with prognosis, molecular alterations, and chemotherapy benefit, but its semantic perturbations remain computational experiments rather than biological perturbations [61] (Table 2). These outputs merit the term biological insight only when they generate falsifiable experiments—for example, CRISPR perturbation of a predicted regulator, orthogonal spatial confirmation of a ligand–receptor interaction, or prospective testing of a response-associated immune programme.

Protein structure, neoantigens, and immune recognition

Protein-structure foundation models provide enabling infrastructure for cancer biology and drug development. AlphaFold and RoseTTAFold markedly improved protein-structure prediction, and AlphaFold 3 extended prediction to biomolecular complexes [99, 102, 113]. Their direct oncology value depends on the downstream question: resolving an uncharacterized target or complex can guide mutational interpretation and compound design, but predicted structure alone does not demonstrate target dependency, druggability, or therapeutic index.

Neoantigen discovery illustrates a similarly layered evidence chain. MHCflurry incorporates antigen processing into peptide-presentation prediction; consortium data have clarified determinants of epitope immunogenicity; BigMHC transfer-learns immunogenicity after presentation training; and pMTnet, NetTCR-2.0, and TITAN model T-cell-receptor–peptide–MHC recognition [97, 98, 101, 104, 106, 109]. These models can prioritize candidates and reduce experimental search space, but performance depends on allele coverage, negative-example construction, assay heterogeneity, and the difference between binding, presentation, recognition, and effective tumor killing. Validation must therefore progress through immunopeptidomics, T-cell assays, tumor-context testing, and ultimately clinical immunogenicity.

Treatment-response prediction and biomarker development

Treatment-response models sit between diagnosis and intervention and remain less mature than image-based detection. Retrospective studies often define response differently, combine small and imbalanced cohorts, and perform feature selection before data splitting. Stronger designs use independent centers, trial cohorts, prospective silent testing, or explicit human–model interaction. A prospective multicenter study in rectal cancer, for example, evaluated interpretable AI assistance rather than model performance alone [134]. Multimodal CT biomarkers have predicted response to neoadjuvant immunochemotherapy in NSCLC, while quantitative ultrasound has been evaluated in a randomized phase II breast-cancer trial [141, 182].

In neuro-oncology, an automated volumetric MRI framework was trained in 455 patients and tested on 2,034 scans from 532 patients across 34 institutions in EORTC-26,101 [179]. Automated time to progression was more reliable than local-versus-central RANO assessment and more strongly associated with overall survival, yet the analysis remained retrospective and the reported survival association does not show that using the model improves management. This study is instructive because it advances endpoint reproducibility without collapsing quantitative measurement, surrogacy, and clinical utility into a single claim.

Pathology-derived predictive biomarkers are now being tested in stronger clinical datasets. Post-hoc analyses of ENZAMET, CHAARTED, and STAMPEDE used randomized phase III trial material to evaluate prognostic or treatment-interaction signals in prostate cancer [89, 91, 135]. A separate classifier using tumour–immune spatial interactions and nuclear heterogeneity showed statistically significant treatment interactions for docetaxel in retrospective analyses of CHAARTED and NRG/RTOG 0521 specimens [183]. A pancreatic-cancer histology biomarker was developed in a multi-institutional cohort and validated in prospective observational cohorts rather than a randomized treatment-assignment study [92]. Trial-derived specimens improve endpoint and treatment consistency, but a retrospective interaction—even when replicated across trials—does not establish benefit from prospective biomarker-guided treatment.

Graph learning and AI-enabled drug discovery

Graph and multimodal drug-response models typically encode molecular structure together with cancer-cell-line omics. DeepSynergy predicted drug combinations from chemical and transcriptomic features; DrugCell imposed a hierarchy of biological subsystems; DeepCDR and DeepDDS used graph neural networks for response or combination prediction; and TranSynergy sought pathway-level interpretability [63, 71, 76, 77, 180]. These benchmarks are useful for prioritization, but in-vitro response labels, incomplete target annotations, and cell-line domain shift limit clinical inference.

Generative chemistry extends prioritization to molecule design. ReLeaSE demonstrated reinforcement-learning generation optimized for specified properties; GENTRL-like deep generative workflows rapidly identified DDR1 inhibitors; and equivariant diffusion models generate three-dimensional ligands conditioned on binding pockets [62, 80, 185]. None bypass synthesis, biochemical confirmation, selectivity testing, pharmacokinetics, toxicology, or clinical development.

Several AI-associated oncology candidates have reached early clinical testing. XL309/ISM3091, a USP1 inhibitor, is recruiting in a phase 1 advanced-solid-tumor study, and ISM3412, a MAT2A inhibitor, is recruiting in a phase 1/2 study [190, 191]. EXS-21,546, an A2A-receptor antagonist, entered phase 1b/2a combination testing with PD-1 inhibition, but the six-participant study was terminated because emerging data indicated difficulty achieving a suitable therapeutic index [192]. Clinical entry demonstrates that computational design can feed a regulated development pipeline, not that efficacy or safety has been established; the EXS-21,546 experience shows that faster design does not eliminate attrition in human development. The widely cited TNIK inhibitor rentosertib/ISM001-055 concerns idiopathic pulmonary fibrosis and should not be presented as an oncology clinical example (Fig. 1).

Fig. 1.

Translational pipeline of AI in oncology drug discovery. Overview of computational prioritization and generative design models (left), mandatory preclinical validation steps (center), and early clinical trial outcomes and limitations(right), highlighting that faster in silico design does not eliminate human clinical attrition

AI in radiotherapy

Radiotherapy is comparatively mature at workflow-level automation. Deep learning has been evaluated for organ-at-risk segmentation, target delineation, dose prediction, plan generation, and treatment adaptation. A 3D U-Net segmented 21 head-and-neck organs at risk with performance approaching expert variability, whereas external and multicentre studies demonstrated organ- and institution-specific differences [123, 125, 130]. A blinded randomized workflow study reported substantial reductions in contouring and revision time after oncologist review, supporting augmentation rather than autonomous acceptance [128]. Multimodal LLM-based target-volume contouring extends automation from anatomy toward clinical reasoning, but reproducible geometric agreement is still upstream of dosimetric safety [163].

Dose prediction and planning studies further illustrate the importance of the endpoint. OpenKBP standardized a 3D dose-prediction benchmark, and anatomy-to-dose models showed technical feasibility [122, 126]. In prospective prostate-planning deployment, most machine-generated plans were clinically acceptable, frequently selected over human plans, and produced faster planning [187]. A 2026 prospective multicenter thoracic auto-segmentation study and a glioblastoma dose-escalation pilot extend evaluation toward real-world use [132, 156]. Still, geometric similarity and planning time are surrogate endpoints; editing burden, dosimetric consequences, treatment delivery errors, toxicity, local control, and survival remain the clinically relevant outcomes (Fig. 2).

Fig. 2.

Evidence landscape and endpoint hierarchy of AI in radiotherapy. Workflow automation in anatomy delineation and dose planning demonstrates high maturity and efficiency gains (left) but relies primarily on surrogate computational metrics. Translation to clinical impact requires validating these models against true patient-centered endpoints, including reduced toxicity, treatment accuracy, and long-term survival (right)

AI in surgical oncology

Surgical AI has focused on rapid tissue characterisation, image guidance, and margin assessment (Table 3). In a multicentre prospective non-inferiority study of 278 patients, stimulated Raman histology with deep learning produced a brain-tumour diagnosis in under 150 s and achieved 94.6% accuracy, compared with 93.9% for pathologist interpretation of conventional intraoperative histology [137]. This is stronger evidence than a retrospective segmentation benchmark, but the system was evaluated as a diagnostic pathway, not as proof of improved extent of resection or survival. In Mohs surgery, ArcticAI combined convolutional and graph neural networks to localise basal-cell carcinoma and map histology to the surgical site; a subsequent workflow simulation estimated staffing and processing effects without demonstrating reduced recurrence or re-excision [139, 140]. Ex-vivo ultrasound segmentation predicted close margins in breast lumpectomy specimens, but the single-centre cohort did not test patient outcomes [138].

Table 3.

Comparative translational maturity across artificial-intelligence oncology domains

Domain	Strongest current evidence	Why the domain has progressed	Remaining translational gap
Mammography/colonoscopy	Large randomized screening and diagnostic-workflow trials	Standardized inputs, immediate labels, established workflow	Program-specific calibration, overdiagnosis, long-term outcomes
Digital pathology	Multinational challenge, external validation, prospective silent deployment	Whole-slide archives, reusable labels, second-reader workflow	Scanner/stain shift, prospective outcome benefit, subgroup errors
Radiotherapy	External auto-contouring, prospective planning integration	Structured planning data and measurable editing/time endpoints	Dosimetric safety, adaptive use, toxicity and tumor-control outcomes
Surgical AI	Prospective imaging and early randomized guidance studies	Real-time visual tasks and defined operative decisions	Single-center datasets, integration burden, recurrence/reoperation outcomes
Treatment-response prediction	Multicenter retrospective and trial-cohort biomarker analyses	Rich imaging and molecular correlates	Heterogeneous endpoints, temporal leakage, prospective treatment assignment
Multi-omics/foundation biology	Large-scale pretraining and cross-cohort benchmarks	Public molecular atlases and self-supervision	Causal validation, batch effects, missing modalities, clinical actionability
Drug discovery	Prospective synthesis pipelines and early clinical candidates	Large chemical spaces and differentiable generative objectives	Selectivity, pharmacology, toxicity, and clinical efficacy
LLM decision support	Prospective concordance, grounded agents, controlled communication studies	Readily available text and flexible interfaces	Hallucination, temporal drift, privacy, automation bias, patient outcomes
Toxicity/survivorship	Large monitoring RCTs; early ML toxicity models	Repeated symptoms and EHR data	Rare-event calibration, alert burden, incremental value over rule-based systems

Synthesizes the translational stage, drivers of progress, and critical implementation gaps across key clinical and biological applications of AI in oncology (including screening, pathology, radiotherapy, surgical guidance, treatment-response prediction, multi-omics/foundation models, drug discovery, large language model decision support, and toxicity/survivorship monitoring). Each domain is evaluated by its highest tier of current clinical evidence, key enablers of development, and the remaining barriers to definitive clinical adoption and prospective outcome benefit

Abbreviations: AI, Artificial intelligence, EHR Electronic health record, LLM Large language model, ML Machine learning, RCT Randomized controlled trial

More recent prospective evidence broadens the field. Smartphone-based resection images were used for multicenter prediction of invasiveness in stage IA lung adenocarcinoma; AI-guided three-dimensional augmented reality was tested in the randomized RIDERS prostatectomy trial; and a machine-learning-guided ileostomy strategy was evaluated in a randomized rectal-cancer surgery study [133, 143, 144]. These trials are more informative than segmentation accuracy alone because they evaluate how AI changes an operative decision or workflow (Fig. 3).

Fig. 3.

Evidence spectrum of AI in surgical oncology. Diagnostic tools and image segmentation models (left) show strong technical accuracy and workflow efficiency but lack proof of improved patient survival or recurrence. Recent prospective and randomized trials (right) evaluate how AI directly alters intraoperative decisions and surgical strategies, marking a shift toward patient-outcome validation

Large language models in oncology

LLM evidence should be separated into knowledge benchmarks, information extraction, patient communication, and decision support. Foundational medical LLMs such as Med-PaLM demonstrated that language models can encode substantial clinical knowledge, and GatorTron showed large-scale representation learning from electronic health records [157, 159]. In oncology, generalist models have produced plausible recommendations and patient answers, but performance varies by prompt, cancer, guideline, and evaluator [164, 170, 188].

Clinical grounding materially changes the task. Retrieval-augmented or case-grounded systems have been developed for precision-oncology recommendations, tumor-board concordance, and hematologic malignancies [160, 172, 175]. HemaGuide, for example, combined guideline pathways with more than 2,000 tumor-board cases and reported external and prospective silent validation; hallucinations were uncommon but not absent. Trial-matching tools have also undergone pragmatic or prospective evaluation [166, 178].

Controlled studies demonstrate both utility and boundaries. LLM-based simplification of oncologic CT reports has been prospectively tested, and a randomized counseling intervention evaluated psychological outcomes [165, 168]. Prospective blinded comparisons against tumor boards in urologic and mixed oncology settings directly assess concordance rather than examination accuracy [174, 176]. Concordance is still not equivalent to improved survival, reduced toxicity, or better shared decision-making. Grounded evidence retrieval, source display, privacy controls, uncertainty communication, escalation rules, and clinician accountability remain mandatory (Fig. 4).

Fig. 4.

Landscape and outcome framework for LLMs in oncology. Foundational medical models (Panel 1) and clinical Retrieval-Augmented Generation (RAG) systems (Panel 2) provide specialized knowledge and workflow support. Controlled evaluations (Panel 3) assess report simplification, counseling, and tumor-board concordance. Crucially, computational agreement does not equate to clinical utility; real-world deployment requires mandatory safety guardrails, grounded evidence, and clinician accountability (Panel 4)

Toxicity prediction, symptom monitoring, and survivorship

Toxicity models often face rare outcomes and repeated measurements. An ePRO-based gradient-boosting study used 820 questionnaires from 34 patients and 26 immune-related adverse events; the high reported AUROC contrasted with only 17 positive onset observations in the test set and patient-observation-level splitting [147]. A national claims analysis addressed severe immune-related adverse events at larger scale but remained vulnerable to coding error, treatment-era drift, and calibration shift [149]. Radiotherapy studies now integrate radiomics, dosiomics, and plasma proteomics to predict pneumonitis, while multi-toxicity models attempt joint normal-tissue complication prediction [131, 136, 155].

Digital symptom monitoring has stronger outcome evidence than AI-specific symptom prediction. eRAPID improved early physical well-being and self-efficacy without reducing admissions or chemotherapy delivery; PRO-TECT improved symptom control, function, quality of life, and emergency utilization without an overall-survival advantage; and web-based lung-cancer surveillance reported a survival difference in a smaller trial [146, 148, 151]. These studies establish the value of structured, timely patient-reported information. They do not establish that adding machine learning improves the system. AI-enhanced monitoring should be compared directly with rule-based ePRO workflows using time to action, grade 3 or higher toxicity, false-alert burden, unscheduled care, quality of life, and equity (Fig. 5) (Table 3).

Fig. 5.

Methodological challenges and evaluation framework for AI in toxicity prediction and digital symptom monitoring. Conceptual overview summarizing current limitations and future directions in cancer toxicity prediction and symptom monitoring. Toxicity Prediction Models (Left): Key methodological vulnerabilities include data leakage from patient-observation-level splitting, rare event bias, and administrative data drift (e.g., coding errors, calibration shift). Advanced multi-toxicity approaches integrate multi-omic and radiomic data to predict joint normal-tissue complications. Digital Symptom Monitoring Evidence (Center): Summarizes evidence from key trials showing improved physical well-being, quality of life, and emergency care utilization, but highlights the distinction between ePRO workflow benefits and added AI value. Proposed Evaluation Path (Right): Recommended metrics for head-to-head clinical trials comparing AI-enhanced monitoring against standard rule-based ePRO workflows

Real-world translation, authorization, and investigational deployment

Paige Prostate received FDA De Novo authorization as an adjunctive pathology device for prostate-biopsy review, not an autonomous primary-diagnosis system [193]. ArteraAI Prostate was authorized as a prognostic tool, and ArteraAI Breast received 510(k) clearance for estimating distant-metastasis risk in HR-positive/HER2-negative early breast cancer [194, 195]. Mammography systems including ProFound AI and Saige-Dx have 510(k) clearances for concurrent reading [196, 197]. The FDA’s AI-enabled device list documents a rapidly expanding portfolio but explicitly notes that the list is not comprehensive and that authorization records must be interpreted in relation to intended use and supporting evidence [198].

Authorization is a regulatory status, not a comparative-effectiveness result. A large empirical audit found that many authorized AI health tools lacked published clinical validation [189]. Before adoption, institutions should examine the exact indication, comparator, external-validation population, subgroup performance, calibration, human-factors testing, update policy, cybersecurity, monitoring plan, and local workflow. Local silent testing and prospective post-deployment surveillance may be more informative than the number of authorizations.

Reported advantages

The advantages supported by the evidence are specific: increased detection in selected screening settings, lower reading or contour-editing burden, more reproducible quantitative assessment, representation transfer when annotation is scarce, integration of complementary data, and prioritisation of biological or chemical hypotheses that would be impractical to enumerate manually. Benefit is most credible when AI augments an established workflow, the reference standard and operating threshold are explicit, external data are available, and evaluation measures clinical decisions, workload, or patient outcomes rather than discrimination alone. Randomized mammography and colonoscopy studies, prospective radiotherapy planning, multicentre intraoperative brain-tumour diagnosis, large-scale weakly supervised pathology, and silent deployment of an H&E-derived EGFR biomarker exemplify progressively stronger forms of evidence [9, 42, 46, 86, 137, 187] (Table 3).

Reported disadvantages and limitations

The corresponding liabilities are unstable transportability, uncertain threshold utility, weak or misleading explanations, demographic and institutional bias, privacy and governance burden, and continuing maintenance after deployment. Scanner, stain, acquisition, population, label, workflow, and treatment-era shifts can degrade performance through different mechanisms and should not be collapsed into a generic failure of “generalizability.” AUROC can coexist with miscalibration, low positive predictive value, excess alerts, or no net clinical benefit; LungIMPACT and negative colonoscopy trials demonstrate that pathway effect cannot be inferred from model accuracy [11, 12, 36]. Site signatures and subgroup disparities can encode non-biological shortcuts, explanation methods may be unstable, and LLM fluency can magnify outdated or unsupported recommendations. Regulatory authorization does not establish comparative effectiveness, while multimodal systems create unresolved questions of consent, ownership, security, accountability, and post-update surveillance [13, 14, 189, 199, 200].

Discussion

Translation is determined by the task, not the size of the model

The principal divide in oncology AI is not between deep learning and conventional methods, or between task-specific and foundation models. It is between tasks whose data-generating process is sufficiently stable for evaluation and tasks in which the target changes with clinical context. Mammography, colonoscopy, pathology review, and radiotherapy contouring offer digitised inputs, comparatively immediate reference standards, and established workflows in which an algorithm can act as a triage system, concurrent reader, or draft generator (Table 3). These conditions made randomized evaluation feasible: MASAI measured interval cancers, sensitivity, specificity, and workload; colonoscopy trials measured adenoma detection; and radiotherapy studies measured contour editing and plan selection [9, 46, 128, 187].

Treatment-response and multi-omics models confront a less stable problem. Response is delayed, treatment-dependent, and distorted by adherence, subsequent therapy, competing risk, and non-standard assessment. Molecular cohorts are smaller than image archives, assays change, and modalities are often missing for reasons related to prognosis or access. A sophisticated fusion architecture can therefore be optimized against a target that differs between institutions or eras. Trial-derived specimens improve outcome definition and treatment consistency, but retrospective treatment-interaction analyses remain vulnerable to missing tissue, post-randomization selection, multiplicity, and thresholds chosen after observing outcomes. The appropriate next experiment is not another retrospective AUROC comparison; it is a locked, assay-defined, prospective study in which the model changes treatment and the clinical consequences are measured.

This distinction explains why pretraining scale has an asymmetric effect. Large corpora improve representation transfer and label efficiency, as demonstrated by UNI, Virchow, Prov-GigaPath, CHIEF, and vision–language pathology models [54, 55, 78, 79, 82]. They do not stabilize an ambiguous endpoint, correct biased labels, or create a clinically appropriate intervention. Foundation models lower the cost of building downstream systems; they do not lower the evidentiary standard for using them.

Generalisation failure is plural and should be diagnosed accordingly

“Dataset shift” is often used as if it were a single technical defect. In practice, several shifts operate through different mechanisms. Acquisition shift arises from scanner hardware, reconstruction, staining, tissue processing, sequencing platform, or report template. Population shift changes prevalence, stage, ancestry, age, comorbidity, and referral spectrum. Label shift reflects different readers, assays, guidelines, or follow-up windows. Workflow shift changes which cases are presented to the model and how its output affects subsequent observations. Temporal or concept drift occurs when therapies, diagnostic criteria, and clinical behaviour evolve. These mechanisms demand different remedies: colour normalization will not correct referral-spectrum bias, recalibration will not repair label leakage, and a larger model will not resolve an intervention aimed at the wrong pathway step.

The reviewed evidence makes these distinctions concrete. Mirai transferred across countries but was developed on a single mammography platform; PANDA showed localised overgrading under cross-continental distribution shift; prospective mammography deployment required threshold recalibration; and computational pathology models can identify site-specific signatures unrelated to tumour biology [5, 13, 38, 51]. EAGLE is informative because performance differed between primary and metastatic specimens and by metastatic site despite multinational and multiscanner validation [86]. Such findings should not be relegated to limitations: they define the intended-use population.

External validation should consequently state what changed and what did not. Testing a frozen model in one additional archive is weak evidence if acquisition, prevalence, labels, and workflow remain similar. Strong validation quantifies calibration and threshold performance, reports prespecified subgroups, describes missingness and exclusions, and analyses discordant cases. After deployment, validation becomes a longitudinal safety function. Model version, data provenance, abstentions, overrides, subgroup errors, calibration drift, and downstream actions need auditable monitoring with predefined triggers for recalibration, restriction, or withdrawal.

Clinical utility begins where discrimination ends

AUROC is useful for comparing ranking performance but is indifferent to calibration, prevalence, action thresholds, and the consequences of false decisions. A clinically interpretable report should include calibration-in-the-large and slope, sensitivity and specificity at prespecified thresholds, positive and negative predictive values at deployment prevalence, and net benefit when a decision threshold is defensible. Rare-event applications—including pancreatic-cancer detection and severe-toxicity prediction—are particularly vulnerable to apparently high AUROC alongside low positive predictive value. For workflow systems, time saved should include correction, false alerts, escalation, and displaced labour. For treatment models, the relevant estimand is the outcome under model-guided care compared with usual care.

LungIMPACT exemplifies the value of pathway-level evaluation. AI prioritisation changed worklist ordering but did not shorten time to computed tomography, diagnosis, referral, treatment, or improve stage at diagnosis; the model acted upstream of other rate-limiting steps [12]. Negative colonoscopy trials provide a related lesson: when expert baseline detection is high, the incremental effect of computer-aided detection may be small or absent [11, 36]. These are not merely negative studies. They identify effect modifiers—baseline performance, prevalence, workflow, and surveillance intensity—that should shape deployment and trial design.

The phrase “comparable to expert clinicians” obscures these issues. Liu and colleagues found that few medical-imaging studies compared AI and clinicians on the same cases under matched conditions, and external validation was uncommon [201]. Nagendran and colleagues similarly documented high risk of bias, scarce prospective or real-world evaluation, and limited access to data and code [202]. A defensible comparison must specify reader expertise, case spectrum, assistance condition, reference standard, operating threshold, external site, and endpoint. Parity on curated cases does not establish autonomous readiness, and superiority in stand-alone accuracy does not establish superiority of the human–AI system.

Biological insight requires a chain of evidence

AI can contribute to molecular oncology at four distinct levels. First, it can identify an association, such as a histological pattern linked to mutation or outcome. Second, an interpretable representation can connect that association to cellular neighbourhoods, pathways, or regulatory programmes. Third, a model can predict an unseen perturbation, interaction, or therapeutic vulnerability. Fourth, the prediction can be tested by orthogonal measurement, genetic or pharmacological perturbation, rescue, in-vivo modelling, and ultimately clinical validation. Only the latter stages warrant strong mechanistic language.

Single-cell and spatial models move the field beyond static classification because their outputs can specify experiments. Geneformer, scGPT, scFoundation, and RegFormer encode regulatory structure; scGen, compositional perturbation autoencoders, and GEARS predict transcriptional responses; Tangram, cell2location, and graph-based spatial methods reconstruct tissue organisation [7, 96, 100, 107, 110, 112, 114, 115, 121] (Table 2). Their value is the capacity to shorten the path from observation to perturbation. Their limitation is that transcriptional agreement may not predict protein activity, phenotype, drug response, or a stable state in vivo.

Spatial pathology makes the same boundary visible. CANVAS and PathPrism translate tissue architecture into cellular neighbourhoods or semantic biomarkers that can be examined across cohorts [61, 117]. These constructs can reveal reproducible ecological patterns and generate hypotheses about immune exclusion or treatment benefit. A virtual whole-slide perturbation, however, is not equivalent to perturbing the tumour ecosystem. Orthogonal spatial assays, lineage-aware experiments, and functional manipulation are required to distinguish a causal interaction from a stable correlate.

Protein-structure and neoantigen models also sit within an evidence chain. AlphaFold and RoseTTAFold can constrain structural hypotheses, and peptide-presentation or T-cell-receptor models can reduce experimental search space [98, 99, 101, 102]. They cannot establish target dependency, druggability, presentation, T-cell killing, or therapeutic index. Similarly, predicted synthetic lethality requires genotype-specific interaction assays, rescue, and in-vivo confirmation. The most credible claim is therefore that AI makes biological discovery more selective and experimentally tractable—not that computation replaces mechanisms.

Foundation models change the unit of validation

Foundation models introduce risks that task-specific validation alone cannot detect. Pretraining datasets can contain duplicated patients, hidden institutional clustering, demographic imbalance, uncertain licences, and future benchmark material. A downstream model may appear externally robust because the test distribution was represented during pretraining. Data lineage and overlap analysis are therefore part of validity, not administrative metadata. Model reports should disclose patient and institution counts, temporal coverage, modality and scanner composition, curation, deduplication, benchmark-overlap checks, and the extent of weight or code access.

The unit of evaluation also shifts from one model to a model family. The same encoder can support diagnosis, biomarker prediction, retrieval, report generation, or prognosis, each with different harms and operating thresholds. A strong average across dozens of benchmarks can conceal unsafe performance in one clinically consequential use. Conversely, the ability to abstain may be more valuable than a small increase in mean accuracy. CHROMA’s risk-control mechanism and EAGLE’s restriction to primary specimens illustrate how intended-use constraints can be designed around observed failures rather than treated as evidence of weakness [86, 87].

Comparing representative foundation models makes the validation gap explicit: corpus scale spans millions of images, slides, or patches, but prospective evaluation remains uncommon and none of the compared studies measured clinical-decision or patient-outcome impact [53–56, 78, 79, 86, 87, 142]. Pretraining scale should therefore be reported as a development attribute, not used as a proxy for translational maturity.

Human–AI systems, not isolated algorithms, are the intervention

Across the most mature domains, the supported use case is augmentation. AI can triage mammograms or slides, propose contours, retrieve evidence, identify trial candidates, or draft patient-facing text while a clinician retains responsibility. Yet human oversight is not a universal safeguard. Poor interfaces can induce automation bias, reduce independent search, or obscure uncertainty; excessive alerts can displace attention; and ambiguous accountability can delay correction. The interface, training, override pathway, escalation rule, staffing model, and audit process are components of the intervention and should be evaluated as such.

LLMs amplify this requirement because fluent language can mask uncertain evidence (Table 3). Retrieval grounding, tumour-board exemplars, and constrained guideline pathways improve factuality, but output remains sensitive to source currency, retrieval failure, prompt framing, local practice, and model updates. Prospective concordance or report-simplification studies are more informative than examination scores, but concordance is not a patient outcome [165, 172, 175, 176]. Safe deployment requires source display, version logging, privacy controls, uncertainty communication, human confirmation of actionable recommendations, and explicit responsibility for monitoring and correction.

Regulatory authorization answers a narrower question than adoption. It establishes that a product meets the requirements of a specified pathway and intended use; it does not establish superiority to local practice, transportability to a new population, or durability after model and workflow updates. The finding that many authorized AI devices lack published clinical validation reinforces the need for evidence-based procurement [30, 189]. Institutions should define clinical problems and baseline performance before purchase, perform silent local testing, prespecify acceptable error trade-offs and subgroup metrics, and maintain withdrawal criteria. Where the model changes care, cluster-randomized, stepped-wedge, or adaptive implementation designs may be more informative than another retrospective benchmark.

An evidence agenda for precision oncology

The next phase of oncology AI should be organised around claim-matched evidence. Diagnostic systems require geographically and temporally external validation, local calibration, human-factors testing, and prospective impact studies. Treatment-selection models require locked assays, prespecified thresholds, treatment-by-biomarker interaction testing, and trials of model-guided care. Molecular foundation models require provenance and overlap audits, cancer-relevant benchmarking, and functional validation of generated hypotheses. LLMs require grounded source evaluation, longitudinal testing after model updates, and measurement of clinician and patient outcomes (Table 3). All deployed systems require post-market surveillance capable of detecting performance and equity drift.

Evaluation should also become more economical and more informative. Multicentre silent deployment can identify acquisition and workflow shift before clinical exposure. Prospective–retrospective analyses of completed randomized trials can test predictive hypotheses when specimens and treatment assignment are appropriate but should lead to prospective validation rather than become an endpoint. Federated or privacy-preserving collaborations may broaden external evaluation, provided that site heterogeneity is analysed rather than averaged away. Reporting frameworks including TRIPOD + AI, PROBAST + AI, CLAIM, DECIDE-AI, and CONSORT-AI provide a minimum structure for transparent reporting [16–20]. The substantive standard is higher: a study should make clear what decision changes, for whom, at what threshold, under whose accountability, and with what evidence of benefit.

Limitations of this review

This review has limitations. Embase, Scopus, and Web of Science were not searched. The synthesis is therefore not an exhaustive evidence census, and the distribution of included studies should not be used to estimate field-wide practice. Heterogeneity across diagnostic studies, prediction models, randomized trials, preclinical benchmarks, and regulatory records precluded a common risk-of-bias instrument or pooled estimand. Quantitative claims emphasised in the text and tables were checked against accessible primary reports, but incomplete reporting limited comparison of sample size, calibration, subgroup performance, missingness, and code availability. Finally, the search was updated to 21 July 2026; trial, authorization, and publication status will continue to change.

Conclusions

AI in oncology should not be judged as a single intervention. It is a collection of models embedded in different biological and clinical systems, each with a distinct failure structure and evidentiary requirement. Randomized and prospective studies now support selected uses in screening, pathology, radiotherapy, surgery, and clinical operations, while negative trials show that technical capability can be neutralised by high baseline performance or an unchanged pathway bottleneck. In molecular oncology, multimodal, single-cell, spatial, structural, and perturbational models are making hypothesis generation more selective and experimentally tractable; most have not yet established mechanism or therapeutic utility.

Progress therefore depends on matching evidence to claim: external testing for transportability, calibration and decision analysis for threshold use, prospective human–AI evaluation for workflow value, randomized studies for patient benefit, and functional perturbation for mechanism. The systems most likely to endure will be those designed around an explicit clinical or biological question, constrained by observed failure modes, and monitored after deployment. Under those conditions, AI can become an accountable instrument of precision oncology rather than a succession of high-performing but weakly translated models.

Authors’ contributions

SKK wrote the first draft, NA prepared the figures, RK and KJ worked on discussion and SA finalized the draft with additional information.

Funding

Not applicable.

Data availability

No datasets were generated or analysed during the current study.

Declarations

Ethics approval and consent to participate

Not applicable.

Consent for publication

Not applicable.

Competing interests

The authors declare no competing interests.