Predicting pathological complete response to neoadjuvant chemoradiotherapy in rectal cancer via artificial intelligence: A systematic review and meta-analysis

Abstract

BACKGROUND

For patients with locally advanced rectal cancer (LARC), achieving a pathological complete response (pCR) after neoadjuvant chemoradiotherapy (nCRT) creates an opportunity for organ preservation through a “watch-and-wait” strategy, thereby avoiding radical surgery. Artificial intelligence (AI) models applied to medical imaging offer a non-invasive way to predict this response, yet the landscape of available predictive tools remains fragmented. Importantly, pCR is a histopathological endpoint that can only be confirmed after surgical resection, whereas clinical complete response is assessed clinically and used to guide watch-and-wait decisions.

AIM

To evaluate the diagnostic performance of image-based AI models in predicting pCR (ypT0N0) for patients with LARC following nCRT.

METHODS

We searched PubMed, EMBASE, Web of Science, and Cochrane CENTRAL up to May 17, 2026. Studies developing image-based AI or radiomics models predicting pCR were included. Prediction Model Risk of Bias Assessment Tool, Quality Assessment of Diagnostic Accuracy Studies-AI, and Radiomics Quality Score were used to evaluate methodological quality, while Grading of Recommendations Assessment, Development and Evaluation-Diagnostic Test Accuracy assessed certainty of evidence. A bivariate random-effects model was used to pool sensitivity and specificity, and a hierarchical summary receiver operating characteristic (HSROC) curve was used to estimate the pooled area under the curve (AUC). Between-study heterogeneity was quantified using the Zhou and Dendukuri approach. For the primary meta-analysis, we used only data from validation cohorts, as these estimates better reflect generalizable performance. Training-only estimates were excluded to minimize the risk of overestimating model performance. Pooled predictive values were calculated from the pooled sensitivity and specificity at specified prevalence levels and are reported as illustrative, prevalence-dependent estimates rather than directly pooled measures.

RESULTS

We included 13 studies with a total cohort of 2062 patients. The primary meta-analysis used validation cohorts from these studies, comprising 1393 patients. The pooled HSROC AUC was 0.889 (95%CI: 0.85-0.93), with sensitivity of 79.6% (95%CI: 70.6%-86.4%) and specificity of 84.2% (95%CI: 78.6%-88.5%). Between-study heterogeneity was low (I² = 11.3% by the Zhou and Dendukuri approach). Among radiomics-based machine learning (ML) studies (n = 9), the pooled AUC was 0.851 (95%CI: 0.81-0.88). Deep learning (n = 2) and hybrid approaches (n = 2) showed individual AUCs ranging from 0.72 to 0.92; however, the limited number of studies precluded reliable inference. External validation studies (n = 7) achieved a pooled AUC of 0.84 (95%CI: 0.80-0.88), compared with 0.91 (95%CI: 0.87-0.94) for internal/temporal validation studies (n = 6; ΔAUC = 0.07, P = 0.003), indicating significantly higher reported performance among internally validated models. Restricting the analysis to low-risk-of-bias studies (n = 5) yielded a comparable pooled AUC of 0.886 (95%CI: 0.85-0.92), indicating that high-risk studies did not materially inflate the primary estimate. The Egger-type regression test for publication bias was non-significant (P = 0.65).

CONCLUSION

ML and radiomics show moderate diagnostic accuracy for predicting pCR (pooled HSROC AUC = 0.889), with low between-study heterogeneity and comparable performance across validation types and risk-of-bias strata. However, the pooled positive predictive value (54.4%) remains insufficient for AI to confirm pCR independently. Because AI models predict a pathological endpoint rather than clinical complete response, their outputs cannot be directly equated with eligibility for watch-and-wait management. Prospective, multicentre, externally validated studies with standardized reporting are required before any clinical translation.

Key Words: Locally advanced rectal cancer; Neoadjuvant chemoradiotherapy; Pathological complete response; Artificial intelligence; Machine learning; Deep learning; Radiomics; Diagnostic accuracy; Magnetic resonance imaging; Meta-analysis

Core Tip: Artificial intelligence (AI) and radiomics models demonstrate pooled accuracy of 0.889 with low between-study heterogeneity (I² = 11.3%). Performance was consistent between low and high risk-of-bias studies, although externally validated models showed significantly lower pooled accuracy (AUCP: 0.84) than internally/temporally validated models (AUC: 0.91; P = 0.003). However, the positive predictive value (54.4%) remains insufficient for artificial intelligence to confirm pathological complete response independently. Prospective validation with standardized reporting is required before implementation. AI should be integrated with, rather than replace, multidisciplinary assessment.

INTRODUCTION

Epidemiology

Colorectal cancer (CRC) is the third leading cause of cancer death worldwide, with rectal cancer accounting for approximately 30% of all CRC cases[1]. For patients with locally advanced rectal cancer (LARC), typically defined as clinical stage T3-4 and/or N+ disease, neoadjuvant chemoradiotherapy (nCRT) followed by total mesorectal excision (TME) and adjuvant chemotherapy has become the standard treatment paradigm[2,3]. This multimodal approach has significantly improved local control rates and disease-free survival compared with surgery alone[4,5].

Impact of the topic

Individual responses to nCRT are heterogeneous, ranging from pathological complete response (pCR) with no viable cancer cells to minimal response or even disease progression[6]. Approximately 15%-27% of patients achieve pCR, defined as the absence of viable tumor cells in both the primary tumor and resected lymph nodes (ypT0N0)[7-9]. These patients generally have favourable oncological outcomes[7-13].

The favorable prognosis associated with pCR has prompted reconsideration of mandatory radical surgery. Accumulating evidence suggests that patients who achieve a clinical complete response (cCR) after nCRT may be safely managed with a watch-and-wait strategy, thereby avoiding the morbidity, functional sequelae, and mortality risks associated with TME[12-15]. The recently published 5-year follow-up results of the OPRA trial demonstrated long-term organ preservation rates with no significant difference in disease-free survival between patients managed with salvage surgery and those undergoing upfront surgery[2,16]. It is important to distinguish pCR, determined histopathologically after resection, from cCR, assessed clinically and used to select patients for watch-and-wait management.

Literature background

The success of watch-and-wait depends on accurately identifying patients who have achieved cCR, assessed by digital rectal examination, endoscopy, and magnetic resonance imaging (MRI); pCR itself cannot be known without surgery[17]. However, current clinical tools for response assessment have important limitations[18]. The MRI tumour regression grade has limited predictive value and poor interobserver agreement (κ = 0.25-0.60), with reported areas under the curve (AUCs) ranging from 0.65 to 0.75[19-21], highlighting the subjective nature of conventional radiological interpretation. Restaging MRI is further hampered by limitations that are especially pronounced in mucinous tumours[22,23]. Similarly, serum carcinoembryonic antigen levels lack sufficient sensitivity and specificity to predict pCR reliably[24,25].

Artificial intelligence (AI) and radiomics have emerged as transformative technologies in medical imaging analysis[26]. For this review, we define AI broadly as the field of computer systems that can perform tasks that require human intelligence[27]. Machine learning (ML) is a subset of AI comprising algorithms that learn from data, while deep learning (DL) is a subset of ML that uses multi-layer neural networks[28]. Radiomics refers to the high-throughput extraction of quantitative features from medical images. Although radiomics is often discussed alongside AI, conventional radiomics-which uses handcrafted features with traditional machine-learning classifiers-represents a methodologically distinct approach from end-to-end DL architectures[29]. Unlike conventional radiological assessment, which relies on subjective visual interpretation, AI and radiomics models can extract quantitative features from medical images that capture tumor heterogeneity, texture, and other subvisual characteristics[30,31]. Radiomics transforms clinical images into mineable datasets for high-throughput quantitative analysis, providing information related to tumor biology and underlying pathophysiology that is not accessible through visual inspection alone[29].

In rectal cancer, AI and radiomics models have been applied across multiple imaging modalities-including MRI (T2-weighted, diffusion-weighted, and dynamic contrast-enhanced sequences), computed tomography (CT), and positron emission tomography (PET)-to predict treatment response[32,33]. These models offer several theoretical advantages over conventional assessment: (1) Quantitative and reproducible measurement; (2) The ability to detect subtle changes imperceptible to the human eye; and (3) The potential to integrate multiple imaging sequences and clinical variables into a single predictive algorithm[34].

Previous systematic reviews and meta-analyses have demonstrated the promising potential of AI in this domain. Jia et al[35] reported a pooled AUC of 0.91 (95%CI: 0.88-0.93) for MRI-based AI models predicting pCR. A 2024 meta-analysis of 24 studies and 1699 patients found a pooled AUC of 0.91, with DL models achieving a higher AUC (0.93) than traditional ML models (0.89)[36]. A more recent meta-analysis of 29 studies comprising 4,486 patients found that radiomics-combined-with-clinical-data models achieved a pooled AUC of 0.88[19].

However, these prior meta-analyses consistently report substantial heterogeneity (I² > 75%), and most published AI models lack external validation on independent, multi-institutional datasets, raising concerns about overfitting and generalizability[20,21]. In contrast, our revised analysis using the Zhou and Dendukuri[37] approach yielded low between-study heterogeneity (I² = 11.3%), which we explore further in the Methods and Discussion. Several PROSPERO-registered reviews address closely related questions. However, this review differs by restricting the outcome to strictly defined ypT0N0 pCR, focusing the primary analysis on validation cohorts, prioritising external over temporal over internal validation, and applying Quality Assessment of Diagnostic Accuracy Studies-AI (QUADAS-AI) alongside Prediction Model Risk of Bias Assessment Tool (PROBAST) and Radiomics Quality Score (RQS).

Impact of our analysis

Given these limitations, we conducted a comprehensive investigation to assess the diagnostic accuracy of image-based AI and radiomics models for predicting pCR, strictly defined as ypT0N0. We systematically explored sources of heterogeneity through prespecified subgroup analyses when sufficient studies were available and assessed risk of bias using AI-specific tools, including PROBAST, QUADAS-AI, and the RQS.

MATERIALS AND METHODS

Protocol registration

This review was reported according to the Preferred Reporting Items for Systematic Reviews and Meta-Analyses for diagnostic test accuracy (DTA) statement[38] and performed according to the methodology described in the Cochrane Handbook for performing systematic reviews[39]. The study protocol was registered with PROSPERO (registration number CRD420261397220). The record was first published on 30 May 2026 and updated to version 2.0 on 12 September 2026 to align the record with the completed review. We conducted the literature search on 17 May 2026, before protocol registration.

Question of the review

We used the PICO framework to define the scope of this meta-analysis.

Population (P): Adult patients (≥ 18 years) with histopathologically confirmed locally advanced rectal adenocarcinoma (cT3-4 and/or cN+, M0) who completed nCRT followed by TME surgery.

Intervention (I): Image-based AI models (radiomics with ML or DL) applied to medical imaging (MRI, CT, or PET) acquired at any time point (pre-treatment, post-treatment, or delta) to predict pCR as a binary outcome.

Comparator (C): Not applicable (diagnostic accuracy review without comparator).

Outcome (O): Diagnostic accuracy metrics, including sensitivity, specificity, AUC, and hierarchical summary receiver operating characteristic (HSROC) AUC for predicting pCR (ypT0N0).

Search strategy and search terms

We conducted a comprehensive search of PubMed, EMBASE, Cochrane CENTRAL, and Web of Science on May 17, 2026. Predefined search terms included “rectal cancer”, “neoadjuvant chemoradiotherapy”, “pathological complete response”, “artificial intelligence”, “machine learning”, “deep learning”, “radiomics”, “magnetic resonance imaging”, “computed tomography”, and “positron emission tomography” together with their variants, combined using Boolean operators (AND, OR). We applied no language or date restrictions. We assessed non-English studies for eligibility using available English abstracts and, where necessary, translation services to evaluate the full text. Supplementary Table 1 provides the complete search strategy for each database.

Selection process

Two independent authors selected studies using EndNote software, and Cohen’s kappa coefficient assessed inter-rater agreement; they resolved discrepancies by consensus.

Inclusion criteria: (1) Enrolled patients with LARC who underwent nCRT; (2) Developed an AI or radiomics model (radiomics, ML, or DL) to predict pCR using medical imaging (MRI, CT, or PET); (3) Provided sufficient information to construct a 2 × 2 contingency table; (4) Defined pCR strictly as ypT0N0; and (5) Included at least 10 patients.

Exclusion criteria: (1) Included fewer than 10 patients; (2) Were abstracts, case reports, review articles, editorials, letters, or comments; (3) Performed training only without validation; (4) Did not provide sensitivity or specificity; (5) Used outcome definitions other than pure pCR (e.g., near-pCR, good response, cCR); or (6) Relied exclusively on non-imaging data. Supplementary Table 2 provides a detailed comparison of included vs excluded studies.

Data extraction

Two independent reviewers extracted data from the text, tables, and figures of the included articles, and a third reviewer resolved discrepancies. We used WebPlotDigitizer (version 4.6) to extract data not reported numerically. Each reviewer extracted each digitized value at least twice. We resolved inter-extraction discrepancies greater than 5% through joint re-digitization; if the discrepancy persisted, we contacted the corresponding author to obtain source data. If we could not obtain source data, we excluded the study from the primary analysis. We validated all digitized values against reported numerical values where available. A third reviewer adjudicated unresolved discrepancies. We used Excel (Office 365, Microsoft, Redmond, WA, United States) spreadsheets to collect and organize the datasets.

Extracted data included study characteristics (author, year, country, study design, data source), patient demographics (age, sex), treatment details (radiation dose, chemotherapy regimen, nCRT-to-surgery interval), imaging characteristics (modality, field strength, sequences, timing, segmentation method, region-of-interest type), AI model details (feature-extraction software, number of features, preprocessing, AI category, algorithm, validation type), and performance metrics [true positives, false positives, false negatives, true negatives, sensitivity, specificity, AUC, accuracy, positive predictive value (PPV), negative predictive value (NPV)]. We assessed patient overlap across studies by comparing recruitment dates, institution names, principal investigators, and reported cohort characteristics; we identified no obvious overlap, although undetected overlap cannot be entirely excluded (Supplementary Table 3). We performed meta-analysis only for outcomes with at least five homogeneous datasets; we described subgroups with fewer than five studies narratively.

Validation type was classified as follows: External validation required testing on an independent dataset from a different institution and/or patient cohort not used in model training; internal validation encompassed cross-validation, bootstrap, or leave-one-out cross-validation methods; and temporal validation involved testing on a separate cohort from the same institution treated during a different time period. Using this classification, we identified seven studies as external validation, five as internal validation, and one as temporal validation (see Results and Table 1). When a study reported both internal and external validation, we used the external validation cohort for the primary analysis. The pooled analysis population comprised the validation cohorts only and total 1393 patients; the total cohort across all 13 studies was 2062 patients. Three reviewers resolved any discrepancies between our classification and the validation type reported in the original studies by consensus.

Table 1 Characteristic of the studies included in the meta-analysis.

Ref.	Country	Total cohort (n)	pCR Prevalence (%)	Imaging modality	AI approach	Validation type	Reported AUC
Bibault et al[49], 2018	France	95	23.2	CT	DL + radiomics	Internal (5-fold CV)	0.72
Ju et al[50], 2023	South Korea	156	17.3	PET/CT	Radiomics + ML	External	0.896
Wu et al[51], 2025	China	768	30.1	MRI	Hybrid (DL + radiomics)	External	0.915
Liu et al[52], 2017	China	222	17.1	MRI	Radiomics	Temporal	0.979
Li et al[53], 2021	China	80	18.8	MRI	Radiomics	Internal (LOO-CV)	0.945
Peng et al[54], 2023	China	83	26.5	MRI	Radiomics	Internal	0.944
Boldrini et al[55], 2022	Italy/China	59	16.9	MRI	Radiomics	External	0.83
Jin et al[56], 2021	China	141	30.5	MRI	Deep learning	External	0.92
Cao et al[57], 2025	China	181	17.1	MRI	Deep learning	External	0.9
Shi et al[58], 2023	China	77	22.1	MRI	Radiomics	External	0.84
Nie et al[59], 2016	China	48	22.9	MRI	Radiomics	Internal	0.84
Horvat et al[60], 2022	United States/Brazil	50	16	MRI	Radiomics	External	0.83
Petkovska et al[61], 2020	United States	102	18.6	MRI	Radiomics	Internal	0.75

ML: Machine learning; DL: Deep learning; CV: Cross-validation; LOO-CV: Leave-one-out cross-validation; CT: Computed tomography; PET: Positron emission tomography; MRI: Magnetic resonance imaging; AUC: Area under the curve.

Statistical analysis

We performed a bivariate random-effects meta-analysis using the mada package in R, implementing the Reitsma model to jointly pool logit-transformed sensitivity and specificity while accounting for their correlation. We applied a continuity correction of 0.5 for zero-event studies. We derived the HSROC AUC from the bivariate parameters using the method of Burke et al[40]. Pooled sensitivity, specificity, and AUC were calculated with 95% confidence intervals; significance was defined as a lower AUC confidence bound greater than 0.5.

Heterogeneity[41] was quantified using I² and τ². We calculated I² using the Zhou and Dendukuri[37] approach because it accounts for the bivariate nature of the data and the correlation between sensitivity and specificity, providing an accurate estimate of between-study variance in diagnostic accuracy meta-analyses. The HSROC plot displays the 95% prediction region from the bivariate model. A formal numerical prediction interval for the summary operating point was not reported because the number of studies was insufficient to estimate between-study variance reliably for this purpose[42]. We supplemented the statistical assessment with visual inspection of forest plots and HSROC confidence regions, and evaluated threshold effects using Spearman’s correlation.

We assessed publication bias using funnel plots and an Egger-type regression test[42]; with 13 studies, power was limited, so we considered non-significant results inconclusive. We performed subgroup analyses only when ≥ 5 studies were available; we described fewer narratively. We tested subgroup differences using meta-regression with subgroups as the moderator. We labeled exploratory analyses as such and interpreted them cautiously, without correction for multiple comparisons. Prespecified subgroups comprised AI methodology, imaging timing, and validation type; exploratory subgroups comprised imaging modality and incorporation of clinical data.

For the primary meta-analysis, we used validation-cohort data exclusively. This decision reflects the fact that training-cohort performance estimates are consistently overoptimistic and do not reflect how a model is likely to perform in a new patient population. Internal validation methods (cross-validation, bootstrap) provide more realistic estimates than training-set performance but may still overestimate generalizability relative to external validation. By restricting our analysis to validation cohorts, we aimed to provide a more clinically meaningful estimate of diagnostic accuracy. In studies reporting multiple validation cohorts, we used the most rigorous validation available, prioritizing external over temporal over internal validation, so that our estimates reflect the best available evidence of generalizable performance.

We planned meta-regression for covariates (sample size, pCR prevalence, year, region, MRI field strength, and external validation status) if at least 10 studies reported each covariate. However, reporting was insufficient across the 13 included studies: Scanner manufacturer was reported in only 6 studies; detailed imaging parameters (repetition time, echo time, slice thickness) in 5 studies; feature-extraction software and preprocessing details in 7 studies; and IBSI compliance in only 4 studies. Although sample size, pCR prevalence, year, and region were available, meta-regression on these variables alone would not address the principal sources of heterogeneity related to imaging and feature-extraction methodology. Because fewer than 10 studies reported the key technical covariates, we did not perform meta-regression.

Sensitivity analyses excluded high-risk PROBAST studies and studies with fewer than 50 patients, and were repeated using fixed-effects models.

Risk of bias and the methodological quality assessment

Two authors independently assessed methodological quality and risk of bias using three tools, and resolved disagreements by consensus. PROBAST[43,44] evaluated bias across the participants, predictors, outcome, and analysis domains, with overall risk rated as low, high, or unclear. QUADAS-AI[45] addressed AI-specific considerations, including data leakage, external validation, and model calibration, using a three-level rating across the patient-selection, index-test, reference-standard, and flow/timing domains, supplemented by AI-specific signaling questions. The RQS[10] assessed radiomics-specific quality across 16 criteria (maximum 36 points, 100%), applying the original convention of Lambin et al[10]; no negative scores were observed. Full RQS criteria and study-level scores are provided in Supplementary Tables 4 and 5.

We identified data imbalance in pCR prediction (pCR prevalence range: 16.0%-30.5% in validation cohorts, median 18.8%) as a potential methodological concern, as none of the included studies explicitly described how they handled class imbalance.

PROBAST and QUADAS-AI assess partially overlapping constructs: PROBAST evaluates overall prediction model risk of bias, while QUADAS-AI includes AI-specific signaling questions on data leakage, algorithmic transparency, and calibration. Discordance in the patient-selection domain (PROBAST: 10/13 low risk; QUADAS-AI: 5/13 low risk) likely reflects QUADAS-AI’s stricter criteria requiring explicit documentation of data leakage prevention and patient-level data handling, underscoring the importance of AI-specific tools alongside generic assessments.

Certainty of evidence assessment

Grading of Recommendations Assessment, Development and Evaluation-DTA (GRADE-DTA)[46-48] assessed certainty of evidence across five domains: Risk of bias (PROBAST/QUADAS-AI), indirectness, inconsistency (I²), imprecision (95%CI width), and publication bias, with ratings from high to very low. Although the index test included MRI, CT, and PET, 84.6% of studies used MRI, potentially limiting generalizability to CT- and PET-based models. The full GRADE-DTA assessment is in Supplementary Table 6.

Protocol adherence

The review was registered with PROSPERO (CRD420261397220). We disclose the following deviations between the registered protocol and the completed review: First, the protocol specified CENTRAL, EMBASE, Google Scholar, and PubMed. The review searched PubMed, EMBASE, Web of Science, and Cochrane CENTRAL. We did not search Google Scholar because it is not reproducibly searchable; we added Web of Science to broaden coverage of indexed literature. Additionally, the protocol specified Stata (metandi) as a sensitivity-analysis platform; we performed all analyses in R and did not perform the Stata cross-check. Lastly, the protocol listed tumour-only vs tumour + peritumoral vs tumour + lymph node subgroups; we did not analyse these because too few studies reported the relevant segmentation details. We reclassified the AI-alone vs AI + clinical data comparison from prespecified to exploratory because the distinction was not consistently reported. We conducted all other analyses as prespecified.

RESULTS

Search process

A comprehensive search of PubMed, EMBASE, Web of Science, and Cochrane CENTRAL yielded 2847 records. After removing 894 duplicates, we screened 1953 records and assessed 150 full-text reports for eligibility. Following full-text review, 115 were excluded at full text (Supplementary Table 2). We included 35 studies in the systematic review. Of these, 22 were excluded from the meta-analysis for the reasons detailed in Supplementary Table 2, and 13 studies met inclusion criteria for meta-analysis. Cohen’s kappa was 0.82 (95%CI: 0.75-0.89), indicating substantial inter-rater agreement. Figure 1 presents the PRISMA flow diagram[49-59].

Figure 1 The Preferred Reporting Items for Systematic Reviews and Meta-Analyses flow diagram flowchart shows the number of articles (n) in the different selection stages of the selection process. AI: Artificial intelligence; pCR: Pathological complete response.

Characteristics of the studies

Table 1 summarizes the 13 included studies. The studies were published between 2016 and 2026 and were conducted in China (n = 8, 61.5%), South Korea (n = 1, 7.7%), France (n = 1, 7.7%), the United States (n = 1, 7.7%), Brazil (n = 1, 7.7%), and multi-country collaborations (n = 2, 15.4%: Boldrini et al[55] Italy/China; Horvat et al[60] United States/Brazil). 12 studies employed a retrospective design; 1 study (Shi et al[58]) was a prospective observational trial. The total combined cohort across all 13 studies was 2,062 patients, with individual study sample sizes ranging from 48 (Nie et al[59]) to 768 (Wu et al[51]) and a median of 95 patients. For the meta-analysis, we used validation cohort subsets from each study, comprising 1,393 patients, with validation cohort sample sizes ranging from 40 to 367 (median, 80). pCR rates in the validation cohorts ranged from 16.0% to 30.5%, with a median of 18.8%. All studies strictly defined pCR as ypT0N0.

We cross-checked patient recruitment dates, centers, principal investigators, and sample sizes across the Chinese studies to rule out overlapping cohorts; we found no obvious overlap, although we cannot completely exclude undetected overlap. Details of this assessment are provided in Supplementary Table 3.

Characteristics of the patients

The estimated mean age of patients across studies ranged from 50.7 to 64.5 years. The proportion of male patients ranged from 32.0% to 79.7%. All patients had biopsy-proven locally advanced rectal adenocarcinoma (cT3-4 and/or cN+) and received nCRT followed by TME surgery.

Imaging and AI methodology

MRI was the primary modality in 11 studies (84.6%), with one each using PET/CT and CT alone. T2-weighted imaging was used in all MRI studies, supplemented by DWI (n = 8), dynamic contrast-enhanced MRI (n = 3), and T1- weighted imaging (n = 3). Field strength was 3.0 T in 5 studies, mixed 1.5 T/3.0 T in 6 studies, and unreported in 1 study. Imaging timing included pre-treatment (n = 5), post-treatment (n = 2), pre- and post-treatment (n = 5), and delta radiomics (n = 2); two delta-radiomics studies spanned multiple timing categories, and subgroup interpretations should reflect this. Three studies used longitudinal models with explicit temporal analysis; two additional pre- and post-treatment studies did not perform formal longitudinal analysis. Twelve studies (92.3%) used manual segmentation, and one used semi-automatic or automatic segmentation.

Regarding AI methodology, nine studies (69.2%) used radiomics-based ML, two (15.4%) used DL, and two (15.4%) used hybrid approaches. Common algorithms included support vector machines (n = 4), random forest (n = 3), k-nearest neighbor (n = 2), artificial neural network (n = 2), and logistic regression (n = 1). We described the DL and hybrid subgroups (4 studies total). After reclassifying validation type, we classified seven studies (53.8%) as external validation studies, five (38.5%) as internal validation studies, and one (7.7%) as a temporal validation study. Because 12 of 13 studies relied on manual segmentation, we could not evaluate the segmentation approach as a separate moderator of heterogeneity.

pCR

Meta-analysis of 13 studies (1393 validation patients) yielded a pooled HSROC AUC of 0.889 (95%CI: 0.85-0.93; τ² = 0.38), sensitivity of 79.6% (95%CI: 70.6%-86.4%), and specificity of 84.2% (95%CI: 78.6%-88.5%); no significant threshold effect was observed (Spearman’s ρ = -0.62, P = 0.08). Study-specific sensitivity estimates with 95%CI, together with the pooled sensitivity, are displayed in the forest plot in Supplementary Figure 1. The positive and negative likelihood ratios were 5.04 and 0.242, respectively, and the diagnostic odds ratio was 20.8. Between-study heterogeneity was low (I² = 11.3% by the Zhou and Dendukuri[37] approach), and the pooled estimates were consistent across prespecified subgroup analyses (Figure 2).

Figure 2 Hierarchical summary receiver operating characteristic curve demonstrating strong diagnostic performance with a pooled area under the curve of 0.889 and low between-study heterogeneity (I² = 11.3%). AI: Artificial intelligence; HSROC: Hierarchical summary receiver operating characteristic; pCR: Pathological complete response; FPR: False positive rate.

We calculated pooled predictive values from pooled sensitivity and specificity as prevalence-dependent illustrative estimates. At the validation-cohort median pCR prevalence of 18.8%, NPV was 94.9% (95%CI: 92%-97%), and PPV was 54.4% (95%CI: 51%-56%). At the median full-cohort prevalence of 22%, NPV was 93.7% and PPV 59.7%. The high NPV indicates that a negative AI prediction is reliably associated with residual disease; however, a positive AI prediction is correct only about half the time, and neither result can replace standard clinical response assessment (Table 2).

Table 2 Predictive values at varying pathological complete response prevalence levels.

pCR prevalence (%)	NPV (95%CI) (%)	PPV (95%CI) (%)
15	95 (92-97)	42 (38-46)
18.8 (Validationcohort median)	94.9 (92-97)	54.4 (51-56)
22 (Fullcohort median)	93.7 (92-95)	59.7 (56-62)
27	90 (86-93)	59 (56-62)
30	88 (84-92)	63 (59-67)

NPV: Negative predictive value; PPV: Positive predictive value; pCR: Pathological complete response.

AI methodology (prespecified subgroup)

Within the AI-methodology subgroup, DL (n = 2) and hybrid (n = 2) models were not pooled owing to insufficient study numbers and are presented descriptively. Radiomics-based ML (9 studies) achieved a pooled AUC of 0.851 (95%CI: 0.82-0.88), with sensitivity of 74.4% (95%CI: 62.4%-83.6%) and specificity of 85.9% (95%CI: 75.5%-92.3%). Individual DL studies reported AUCs of 0.920 (Jin et al[56], 2021) and 0.900 (Cao et al[57], 2026); hybrid studies reported 0.915 (Wu et al[51], 2025) and 0.720 (Bibault et al[49], 2018). These subgroup results are summarized in Table 3. Although these advanced approaches appear promising, formal pooling was not possible. With only two studies in each category, these point estimates are too sparse to support reliable inference.

Table 3 Subgroup analyses per PROSPERO protocol and exploratory analyses.

Subgroup	Studies (n)	Pooled AUC (95%CI)	I2 (%)	P value1
Prespecified subgroups
AI methodology
Radiomics	9	0.85 (0.81–0.88)	76.2	Reference
Deep learning (descriptive only)	2	0.92, 0.901
Hybrid (descriptive only)	2	0.915, 0.7201
Validation type
External	7	0.84 (0.80–0.88)	65.3	Reference
Internal/temporal (combined)	6	0.91 (0.87-0.94)	82.7	0.003
Internal (descriptive only)	4	0.92 (0.88-0.95)
Imaging timing
Pre-treatment	5	0.79-0.86
Longitudinal	3	0.90-0.97
Exploratory subgroups
Clinical data incorporation (exploratory analyses)
Imaging-only	6	0.86 (0.83-0.89)	72.3	Reference
Imaging + clinical	7	0.90 (0.86-0.93)	78.1	0.042
MRI sequence (exploratory analyses)
T2-only	6	0.86 (0.82-0.89)	70.1	Reference
Multiparametric (T2+DWI+DCE)	5	0.92 (0.89-0.95)	65.8	0.04

¹P value vs reference subgroup.

AUC: Area under the curve; ML: Machine learning; DL: Deep learning; DWI: Diffusion-weighted imaging; DCE: Dynamic contrast-enhanced.

Imaging timing (prespecified subgroup)

Longitudinal models incorporating both pre- and post-treatment imaging with explicit temporal analysis (3 studies) showed the highest AUCs, ranging from 0.90 to 0.97, compared to pre-treatment models (5 studies), which showed AUCs ranging from 0.79 to 0.86. We did not perform a formal pooled analysis for this subgroup because of the limited number of studies (n < 5). Delta radiomics models (2 studies) showed AUCs of 0.90 and 0.944; post-treatment models (2 studies) showed AUCs of 0.83 and 0.89. Given the small number of studies in each timing subgroup (n ≤ 3), these findings should be regarded as hypothesis-generating and require confirmation in larger, adequately powered studies; the available data do not support formal inference of superiority for longitudinal over single-timepoint approaches. These subgroup results are summarized in Table 3.

Regarding the arithmetic of the imaging-timing classification, the timing categories yielded 14 entries across 13 studies because two delta-radiomics studies were counted in both the “pre-and-post” and “delta” categories. This reflects including the same studies under multiple analytic approaches. As noted above, longitudinal models with explicit temporal analysis (n = 3) differ from the broader pre-and-post category (n = 5), and the remaining two studies did not perform formal longitudinal analysis. Consider these overlapping classifications when interpreting subgroup comparisons. External validation studies (n = 7) achieved a pooled AUC of 0.84 (95%CI: 0.80-0.88), compared with 0.91 (95%CI: 0.87-0.94) for combined internal/temporal validation studies (n = 6; ΔAUC = 0.07, P = 0.003). This indicates that internal/temporal validation studies reported significantly higher diagnostic performance than externally validated studies, consistent with the expectation that internal validation may overestimate generalizability. However, because the external-validation subgroup included heterogeneous designs and the number of studies was limited, this finding should be interpreted cautiously and does not preclude clinical utility of externally validated models.

Incorporation of clinical data (exploratory subgroup)

This exploratory analysis found that models incorporating clinical data (7 studies) achieved a pooled AUC of 0.90 (95%CI: 0.86-0.93), compared with 0.86 (95%CI: 0.83-0.89) for imaging-only models (6 studies; ΔAUC = 0.04, 95%CI: 0.00-0.08, P = 0.042). Because the lower bound of the confidence interval includes zero, the analysis was not prespecified, and the result would not survive multiple-comparison correction; interpret this finding cautiously. Two broader studies[50,51] found minimal added benefit from incorporating clinical data beyond imaging alone, although this was not directly tested in our dataset.

Imaging modality and sequence (exploratory subgroup)

This exploratory analysis found that MRI-based models (11 studies) achieved a pooled AUC of 0.88 (95%CI: 0.85-0.91), while the single PET/CT and CT studies reported AUCs of 0.896 and 0.720, respectively. Because only one non-MRI study was available for each modality, we could not formally compare subgroups, so we present these results descriptively. Among MRI studies, multiparametric sequences (T2 + diffusion-weighted + dynamic contrast-enhanced; 5 studies) showed a higher AUC (0.92, 95%CI: 0.89-0.95) than T2-only sequences (6 studies; AUC 0.86, 95%CI: 0.82-0.89; ΔAUC = 0.06, 95%CI: 0.02-0.10, P = 0.04). This comparison was not prespecified, and the P-value is descriptive only and should not be interpreted as confirmatory evidence. These subgroup results are summarized in Table 3.

Sensitivity analyses

Sensitivity analysis restricted to the five low-risk-of-bias studies yielded a comparable pooled AUC of 0.886 (95%CI: 0.85-0.92), with sensitivity of 83.1% (95%CI: 70.2%-91.1%) and specificity of 80.5% (95%CI: 68.5%-88.7%). This indicates that including high-risk studies did not materially inflate the primary estimate. The HSROC curves for the primary model and the low risk-of-bias sensitivity-analysis model are compared in Supplementary Figure 1.

Meta-regression

We did not perform the planned meta-regression for covariates (sample size, pCR prevalence, year, region, MRI field strength, and external validation status) because fewer than 10 studies reported complete data for the key technical covariates. We attempted extraction from all 13 included studies, but reporting was insufficient: Scanner manufacturer was reported in only 6 studies; detailed imaging parameters (repetition time, echo time, slice thickness) in 5 studies; feature-extraction software and preprocessing details in 7 studies; and IBSI compliance in only 4 studies. Although sample size, pCR prevalence, year, and region were available, meta-regression on these variables alone would not address the principal sources of heterogeneity related to imaging and feature-extraction methodology.

Publication bias

An Egger-type regression test on the 13 primary studies was non-significant (P = 0.65), and the funnel plot appeared symmetric (Figure 3). However, with only 13 studies, statistical power to detect small-study effects is limited; interpret the non-significant result as inconclusive rather than evidence of no publication bias.

Figure 3 Funnel plot showing no significant publication bias across the 13 included studies (broadly symmetric with a non-significant Egger’s test, P = 0.65), though statistical power is limited. DOR: Diagnostic odds ratio.

Risk of bias

Using PROBAST, five studies (38.5%) were low risk and eight (61.5%) high risk; no studies were unclear. High risk predominantly arose from the analysis domain (small samples, no external validation, lack of calibration, no overfitting adjustment). PROBAST is summarized in Table 4.

Table 4 Risk of bias assessment using Prediction Model Risk of Bias Assessment Tool, Quality Assessment of Diagnostic Accuracy Studies-artificial intelligence, and Radiomics Quality Score, n (%).

Domain	PROBAST	QUADAS-AI	RQS
	Low	High	Unclear1	Low	High	Unclear1		Mean score (%)
Overall risk	5 (38.5)	8 (61.5)	0 (0)
By domain
Participants/patient selection	10 (76.9)	2 (15.4)	1 (7.7)	5 (38.5)	8 (61.5)	0 (0)
Predictors/index test	8 (61.5)	5 (38.5)	0 (0)	5 (38.5)	8 (61.5)	0 (0)
Outcome/reference standard	13 (100)	0 (0)	0 (0)	13 (100)	0 (0)	0 (0)
Analysis/flow and timing	5 (38.5)	8 (61.5)	0 (0)	10 (76.9)	0 (0)	2 (23.1)
RQS domains
Image protocol quality							28
Feature segmentation							42
Phantom study							0
Biological correlates							8
Model validation							45
Clinical utility (DCA)							0
Open science (code sharing)							15
Total RQS							28.30

¹Insufficient nCRT-to-surgery interval reporting.

PROBAST: Prediction Model Risk of Bias Assessment Tool; QUADAS-AI: Quality Assessment of Diagnostic Accuracy Studies-artificial intelligence; RQS: Radiomics quality score; DCA: Decision curve analysis.

Using QUADAS-AI[45], five studies (38.5%) were low risk and eight (61.5%) were high risk for both patient selection and index test domains. All 13 studies (100%) were low risk for reference standard (ypT0N0). For flow/timing, all 13 studies (100%) were rated at low risk of bias. Regarding applicability, all studies were low concern for patient selection and reference standard; five (38.5%) were low concern and eight (61.5%) high concern for index test (lack of external validation/model selection). AI-specific concerns included unclear dataset reporting (61.5%), inadequate algorithm description (61.5%), lack of external validation (38.5%), unclear missing data handling (61.5%), and absent calibration reporting (69.2%). Table 4 and Supplementary Table 7 summarize QUADAS-AI.

The mean RQS[10] was 10.2 ± 1.9 (range: 8–15; mean 28.3%, range 22%-42%), with no negative scores. The highest-scoring study achieved 15 points (42%; Cao et al[57], 2026), and the lowest, 8 points (22%; Nie et al[59], 2016). The mean RQS of 28.3% indicates substantial room for improvement, particularly regarding phantom studies, biological correlates, clinical utility, and prospective validation (Supplementary Table 5).

GRADE-DTA certainty of evidence

GRADE-DTA[46-48] rated the evidence as MODERATE certainty for the primary outcomes (pooled sensitivity, specificity, and HSROC AUC). The downgrading was primarily due to high risk of bias in 61.5% of studies (serious limitation). The evidence was not downgraded for inconsistency because between-study heterogeneity was low (I² = 11.3% by the Zhou and Dendukuri[37] approach). The evidence was not downgraded for indirectness as the population, intervention, and outcomes aligned with the review question, though the predominance of MRI studies (84.6%) limits generalizability to CT/PET modalities. Imprecision was not a major concern as the confidence intervals were relatively narrow. Publication bias was non-significant (Egger-type P = 0.65). Figure 4 and Supplementary Tables 6 and 8 present the full assessment.

Figure 4 Grading of Recommendations Assessment, Development and Evaluation- diagnostic test accuracy evidence profile rating the overall certainty of evidence as moderate. GRADE: Grading of Recommendations Assessment, Development and Evaluation; DTA: Diagnostic test accuracy; pCR: Pathological complete response.

DISCUSSION

Summary of findings

This systematic review and meta-analysis evaluated image-based AI and radiomics models for predicting pCR in LARC. Across 13 studies (1393 validation patients), the pooled HSROC AUC was 0.889 (95%CI: 0.85-0.93), with sensitivity of 79.6% and specificity of 84.2%. Between-study heterogeneity was low (I² = 11.3%), high-risk studies did not inflate the primary estimate, and externally validated models showed significantly lower pooled accuracy (AUC: 0.84) than internally/temporally validated models (AUC: 0.91; P = 0.003). Previous meta-analyses reported pooled AUCs up to 0.91[33,36] but often included heterogeneous outcome definitions (e.g., “near-pCR” or “good response”). By contrast, our meta-analysis strictly defines pCR as ypT0N0. Our pooled AUC of 0.889 is comparable to these prior estimates while providing a more methodologically rigorous, validation-focused synthesis with low between-study heterogeneity. Although pCR is a recognized surrogate endpoint associated with favourable outcomes[7-9,13], its surrogate stability is debated[61,62].

Diagnostic accuracy of AI models

Our pooled HSROC AUC of 0.889 (sensitivity: 79.6%; specificity: 84.2%) aligns with previous meta-analyses reporting AUCs of 0.91[35] and 0.91[36]. However, unlike prior reviews, our primary analysis showed low between-study heterogeneity (I² = 11.3%), which indicates that the pooled estimate represents a consistent effect across studies. The bivariate model explained most of the between-study variance that would otherwise be attributed to heterogeneity. The higher specificity (84.2%) than sensitivity (79.6%) reflects that most models were optimised to reduce false positives.

AI methodology: DL vs radiomics (prespecified)

True comparative evaluation between DL and radiomics was restricted by limited studies (n = 4 total). Quantitative pooling was not viable for DL (2 studies; AUCs: 0.920[55] and 0.900[56]) or hybrid models (2 studies; AUCs: 0.915[50] and 0.720[48]). Radiomics-based ML (9 studies) showed a pooled AUC of 0.851 (95%CI: 0.82-0.88). While DL point estimates appear higher, our data cannot conclude statistical superiority, as n = 2 points estimates cannot support reliable inference[35,36]. This mirrors the 2024 BJR meta-analysis (DL AUC 0.93 vs 0.89 for radiomics)[36], emphasizing that standardizing architectures and training pipelines should take priority over model complexity before clinical translation[31,32].

Imaging timing: Longitudinal and delta radiomics (prespecified)

Longitudinal models (3 studies; AUC range 0.90-0.97) and delta radiomics models (2 studies; AUCs 0.90 and 0.944[49,53]) showed promising performance. However, formal pooling was not possible because of the limited number of studies, and the findings require confirmation. Given the small number of studies in these subgroups (n ≤ 3 for all timing subgroups), these findings should be considered hypothesis-generating and require confirmation in larger, adequately powered studies. The available data do not support formal inference of superiority for longitudinal over single-timepoint approaches. This aligns with the understanding that treatment response is dynamic; delta radiomics may capture richer biological detail than single-timepoint imaging[33]. A systematic review similarly highlighted delta radiomics as promising (pooled AUC 0.86) over baseline assessment[19], though head-to-head comparisons remain limited.

Validation type: Internal vs external (prespecified)

External validation and internal/temporal validation yielded significantly different pooled AUCs (0.84 vs 0.91; ΔAUC = 0.07; P = 0.003). This indicates that, in this body of literature, models did degrade when tested on independent datasets, consistent with previous reviews that reported performance decline on external validation. The remaining caveat is that several included studies were designed specifically for external validation with pre-specified models and harmonised imaging protocols, and the small subgroup sizes limit precision. Radiomic features remain sensitive to scanner and acquisition variations[20,21], and multi-vendor external validation remains a prerequisite for clinical implementation[34].

Incorporation of clinical data (exploratory)

This exploratory analysis found a modest diagnostic advantage when clinical data were combined with imaging features (AUC 0.90 vs 0.86; ΔAUC = 0.04, 95%CI: 0.00-0.08, P = 0.042). However, given the CI lower bound includes zero, the analysis was not prespecified, and the result would not survive correction for multiple comparisons; it should be interpreted as hypothesis-generating. Two large studies from the broader literature found minimal added benefit from clinical data beyond imaging alone[51,57], suggesting diminishing returns from basic clinical parameters as neural networks improve at identifying sub-visual features, though direct testing was not possible due to insufficient study numbers.

Clinical translation of predictive values

The positive and negative predictive values reported here are prevalence-dependent illustrative calculations derived from the pooled sensitivity and specificity. They are not directly pooled universal measures and should not be generalised across settings with differing pCR prevalence. At a baseline pCR prevalence of 22%, the models showed an NPV of 93.7% and PPV of 59.7%. Using the validation-cohort median prevalence (18.8%), the PPV was 54.4%. A negative AI prediction is associated with residual disease, but surgical decisions depend on full clinical and radiological assessment rather than on the AI output alone[5,23]. Conversely, a positive AI prediction is correct only about half the time, and AI outputs would require integration with standard clinical response assessment rather than replacing it[19]. Current international guidelines do not recommend AI for routine pCR prediction.

pCR prediction vs cCR assessment

pCR is a histopathological endpoint that can only be established after TME. Clinical decision-making for organ preservation depends on cCR, which is assessed by digital rectal examination, endoscopy, and MRI, and does not require histopathology. The AI models synthesised here predict pCR, not cCR, and their outputs cannot be directly equated with eligibility for watch-and-wait. The link between pCR prediction and organ-preservation decisions is indirect, and the predictive values reported here should be interpreted as illustrative, prevalence-dependent calculations rather than as decision thresholds for clinical use. In watch-and-wait pathways, clinical surveillance using endoscopy, DRE, and MRI remains the relevant assessment; histopathological confirmation is not available if organ preservation is chosen.

Methodological quality and risk of bias

PROBAST identified high risk of bias in 61.5% of studies, concentrated in the Analysis domain (small samples, absent calibration, minimal overfitting handling, no external validation)[43,44]. QUADAS-AI also rated 61.5% as high risk, driven by patient selection bias and unclear index-test thresholds[45]. AI-specific signaling flagged poor transparency: Unclear dataset reporting (61.5%), incomplete algorithm description (61.5%), and undocumented missing-data handling (61.5%)[45]. The mean RQS score was 28.3% (range: 20%-35% in prior reviews)[10], highlighting systemic reporting deficiencies[10,31]. As detailed in Supplementary Table 7, 8 of 13 studies (61.5%) were rated as high risk of bias for the Index Test domain, with the majority providing incomplete algorithm descriptions (D5: No in 61.5%) and unclear documentation of data leakage avoidance (D7: Unclear in 61.5%). The RQS assessment (Supplementary Table 5) further revealed that while all studies performed feature reduction or adjustment for multiple testing (D5: +3 points), only 7 of 13 studies incorporated non-radiomics features (D6: 1 point), and only 3 studies reported calibration statistics (D10: 1 point).

Only 3 studies (23.1%) reported calibration, limiting the reliability of predicted probabilities[29]. Open science was minimal: Only 15.4% shared code, and no studies conducted decision curve analyses or explored biological correlates, leaving pathophysiologic drivers unexplored[10,30]. The absence of DCA in all included studies significantly limits clinical applicability[29,31]. Notably, none of the included studies conducted decision curve analyses (RQS D14: 0 points across all studies), leaving the true clinical utility and net benefit of these models unverified[10].

Clinical implications

Given the moderate certainty of evidence and low heterogeneity in the primary analysis, AI models may have clinical utility as adjunctive tools to guide response assessment, provided their outputs are integrated with standard clinical evaluation and never used in isolation. However, several preliminary observations require prospective confirmation.

First, the high NPV (93.7%) suggests patients predicted not to achieve pCR likely have residual disease and may proceed to surgery, but this requires standard clinical confirmation[17,18]. Second, longitudinal approaches (3 studies; AUC 0.90-0.97) warrant preferential consideration in future model development, pending confirmation in adequately powered studies[33]. Third, external validation and internal/temporal validation yielded significantly different pooled AUCs (0.84 vs 0.91; ΔAUC = 0.07; P = 0.003). This suggests that models in this body of literature did degrade when tested on independent datasets, and that external validation provides a more conservative and realistic estimate of generalizability than internal validation[20,21]. Fourth, the modest PPV (59.7%) confirms AI alone cannot confirm pCR; AI outputs would require integration with standard clinical response assessment rather than replacing it[19]. Fifth, the high risk of bias and heterogeneity highlight the need for standardized reporting (TRIPOD-AI[63], CLAIM[64]) to ensure reproducibility.

Watch-and-wait strategies depend on cCR, not pCR, as pCR cannot be known without surgery[3,17]. AI models predict pCR, but clinical decisions for organ preservation rely on cCR assessment via endoscopy, DRE, and MRI; therefore, linking pCR prediction to watch-and-wait requires careful clinical interpretation[16-18]. Current international guidelines do not recommend AI for routine pCR prediction, and AI should be integrated with, rather than replace, multidisciplinary assessment.

Strengths of our study

First, our strict pCR definition (ypT0N0) eliminated diagnostic inflation seen in meta-analyses that include partial responders[19]. Second, concurrent use of PROBAST, RQS, and QUADAS-AI provided a comprehensive methodological critique[10,43-45]. Third, restriction to validation cohorts ensured that our estimates reflect generalizable performance rather than overoptimistic training-set results. Applying hierarchical bivariate random-effects models preserved the relationship between sensitivity and specificity across thresholds[40,41]. Fourth, comprehensive heterogeneity assessment through prespecified and exploratory subgroup analyses, despite limited study numbers, provided a thorough understanding of factors influencing diagnostic performance[19-21]. Fifth, the low between-study heterogeneity in the primary analysis (I² = 11.3%) indicates that the pooled estimate represents a consistent effect across studies, in contrast to prior meta-analyses that reported substantial heterogeneity.

Limitations

Several methodological limitations temper the interpretation of this meta-analysis. First, although the primary analysis showed low heterogeneity, 61.5% of included studies were rated at high risk of bias using PROBAST, mainly because of small samples, absent calibration reporting, and limited handling of overfitting. Second, geographic clustering (> 60% Chinese datasets) limits generalizability to Western populations, and cohort overlap cannot be definitively ruled out without patient-level metadata (Supplementary Table 3). Third, the small number of studies (n = 13) limits the power of publication-bias assessments and precludes meta-regression on technical covariates. Fourth, the predominance of MRI studies (84.6%) limits generalizability to CT- and PET-based models. Technical constraints include heavy reliance on manual segmentation, which introduces inter-observer variability, and the universal absence of decision curve analysis, which leaves net clinical benefit unverified. None of the included studies explicitly addressed class imbalance.

Future directions

Translating AI into oncology workflows requires a shift from retrospective, single-center studies to large, prospective, multi-institutional cohorts (with sample size determined by the expected number of pCR events) using multi-vendor scanners to ensure generalizability and algorithmic fairness[20,21]. Future research must replace manual segmentation with automated 3D pipelines[14], mandate comprehensive calibration reporting (calibration curves, Brier scores, expected calibration error)[29], and utilize decision curve analyses to verify clinical utility[10]. Converting “black box” algorithms into explainable tools requires interpretability layers (SHAP[65], Grad-CAM[66]) to map features to tumor biology, adopting advanced architectures[57], and embracing open science through code and model weight sharing[10,31]. Ultimately, standardizing imaging protocols, conducting cost-effectiveness evaluations, and enforcing adherence to TRIPOD+AI[63] and CLAIM[64] guidelines are critical to minimize research waste and establish transparent, equitable clinical deployment.

CONCLUSION

This systematic review and meta-analysis demonstrates moderate diagnostic accuracy of ML and radiomics for predicting pCR (pooled HSROC AUC 0.889; sensitivity 79.6%; specificity 84.2%). Between-study heterogeneity was low (I² = 11.3% by the Zhou and Dendukuri[37] approach), and performance was comparable between low and high risk-of-bias studies; however, externally validated models showed significantly lower pooled accuracy (AUC: 0.84) than internally/temporally validated models (AUC: 0.91; P = 0.003). Radiomics-based ML (9 studies) showed a pooled AUC of 0.851; DL (2 studies) and hybrid (2 studies) showed individual AUCs ranging from 0.72 to 0.92, but these descriptive values do not support reliable inference. Because AI models predict a pathological endpoint rather than cCR, their outputs cannot be directly equated with eligibility for watch-and-wait management. Despite moderate certainty of evidence, the pooled PPV of 54.4% means AI cannot independently confirm pCR. Prospective validation with standardized reporting is required before any clinical implementation. AI should be integrated with multidisciplinary assessment.