médical IA

Early recurrence of hepatocellular carcinoma after radiofrequency ablation: an MRI radiomics model reports an AUC of 0.909, measured on 34 patients and 12 recurrences

Published on August 24, 2026 · 14 min read

Seven authors from the Fourth Medical Center of the Chinese PLA General Hospital in Beijing extracted 11,320 radiomics features from five MRI sequences in 169 patients with hepatocellular carcinoma treated by radiofrequency ablation between 2015 and 2021, then trained three classical machine learning classifiers to predict recurrence within one year. The best of them — a random forest combining 16 LASSO-selected features with three clinical variables — reaches an AUC of 0.975 in training and 0.909 (95% CI 0.807–1.000) on the test set. That test set holds 34 patients including 12 recurrences, it comes from the same centre, the same operator and the same scanners as the training set, and nine models were compared on it before the winner was reported as the model.

The context

Radiofrequency ablation is, alongside resection and transplantation, one of three curative treatments for early-stage hepatocellular carcinoma. An electrode is placed in the tumour under ultrasound or CT guidance, heated, and destroys the tissue by thermal necrosis. The appeal is obvious in cirrhotic patients whose hepatic reserve rules out surgery; so is the limitation: the procedure leaves the liver in place, with its underlying disease and its carcinogenic potential, and intrahepatic recurrence is common. In the cohort described here, 61 of 169 patients, or 36.1%, recur within a year.

Identifying in advance who will recur would have practical value: intensifying surveillance, discussing resection rather than ablation, or directing a patient toward an adjuvant protocol. The existing tools — BCLC staging, CLIP score — are prognostic staging systems designed for populations rather than individuals, and they carry no quantitative information about tumour heterogeneity.

Radiomics is the methodological answer the field has been offering for a decade. The principle: instead of describing a tumour by the handful of attributes a radiologist names (size, capsule, enhancement), thousands of statistical descriptors of voxel intensity and spatial arrangement are computed automatically — first-order moments, co-occurrence matrices, run lengths, all repeated after wavelet or Laplacian-of-Gaussian filtering. The result is a vector of several thousand dimensions per tumour, hoped to capture a biological heterogeneity invisible to the eye. The field's structural problem follows immediately: thousands of variables for a few dozen events, which makes feature selection both indispensable and hazardous.

The method

The cohort. Retrospective, single-centre. Of 486 patients screened between January 2015 and December 2021, 317 were excluded (65.2%): prior anti-tumour treatment, chemoembolisation or systemic chemotherapy (n = 148), macrovascular invasion (n = 61), extrahepatic metastases (n = 68), another malignancy (n = 19), MRI artefacts (n = 21). That leaves 169 patients, all early-stage by the inclusion criteria: a single tumour of 5 cm or less, or multiple lesions each 3 cm or less. The cohort is 89.9% male, median age 58, and 73.9% hepatitis B positive. Diagnosis rests on histology in 37.9% of cases and on imaging per AASLD guidelines in the remaining 62.1%.

The procedure and the endpoint. All ablations were performed by a single interventional surgeon with more than twenty years of experience, Medtronic Cool-tip system, 17-G electrode, twelve minutes per lesion. Early recurrence is defined as any recurrence within twelve months, adjudicated by a radiologist with more than thirty years of experience on imaging or histology, and confirmed in a multidisciplinary meeting. Follow-up mandates liver MRI and chest CT at one month, then every three months for the first year. Ablation was complete at one month in 161 of 169 patients (95.3%); the ablation margin was under 5 mm in 43 patients (25.4%), and that parameter alone is associated with recurrence (OR 2.05; 95% CI 1.01–4.16; P = 0.044). The authors deliberately exclude it from the model: it is a post-procedural datum, unavailable at the moment one would want to predict.

Imaging and features. 3.0-tesla MRI on two machines — GE Discovery 750 (98 patients) and Siemens Skyra (71) — with five sequences used: T2, diffusion, and the arterial, portal venous and delayed phases of the contrast-enhanced dynamic acquisition. Tumour volumes were segmented manually, slice by slice, in ITK-SNAP, by two radiologists, then reviewed by a senior radiologist with more than twenty years of experience. Agreement between the two operators is measured: mean Dice coefficient 0.85 ± 0.06 (range 0.72–0.94), that is, the overlap between their two contours. After Z-score normalisation, isotropic resampling to 1 mm and fixed-bin-width discretisation at 25, 2,264 features per sequence per patient were extracted, 11,320 in total, on a proprietary United Imaging platform.

The selection. Four cascading filters. First: reproducibility between the two segmentations, ICC threshold above 0.75 — 6,965 features survive, or 61.5%. Second: variance threshold, 199 uninformative variables removed. Third: univariate F-test, 1,398 features retained. Fourth: LASSO regression, a penalised regression that forces the coefficients of the least useful variables to zero, with the penalty parameter chosen by ten-fold cross-validation — 16 final features. Their stability is checked with 1,000 bootstrap resamples: 14 of the 16 reappear in more than 80% of draws. Their provenance is detailed (one from T2, one from diffusion, seven from the arterial phase, three from portal venous, four from delayed) but their exact names are relegated to a supplementary table, outside the article text.

Models and split. Three classical algorithms — support vector machine, logistic regression, random forest — applied to three input sets: radiomics only (16 variables), clinical only (3 variables: alpha-fetoprotein above 20 µg/L, platelets at or above 140 × 10⁹/L, and a so-called "special" tumour location, meaning adjacent to the diaphragm, gallbladder, gastrointestinal tract, bile ducts, porta hepatis or the capsule), and integrated (19 variables). No deep learning is used, despite the "AI model" label in the title. Stratified random 80/20 split: 135 patients in training (49 recurrences), 34 in testing (12 recurrences). To their credit, and stated explicitly: normalisation, ICC computation, feature selection and hyperparameter tuning are all performed inside the training set alone, after which the frozen pipeline is applied unchanged to the test set. AUCs compared by DeLong test with Bonferroni correction over six pre-specified comparisons, threshold P < 0.0083.

The results

The three clinical variables. In multivariable analysis on the training set, three predictors emerge: alpha-fetoprotein above 20 µg/L (OR 1.24; 95% CI 1.01–2.56; P = 0.004), platelets at or above 140 × 10⁹/L, which are protective (OR 0.41; 0.17–0.98; P = 0.045), and above all special tumour location (OR 6.41; 2.03–20.24; P = 0.002). The last is by far the strongest, and it is mechanistically plausible: a tumour abutting the diaphragm or the porta hepatis is precisely the one where an adequate ablation margin is hardest to achieve.

The models. Radiomics only: AUC 0.945 to 0.957 in training, 0.826 to 0.830 in testing depending on the classifier, with no significant difference among the three. Clinical only: 0.744 to 0.790 in training — and here an unreconciled inconsistency in the paper, with the abstract and body text reporting test AUCs of 0.688, 0.706 and 0.724 while Table 5 shows 0.600, 0.661 and 0.665. Integrated: the random forest rises to 0.975 (0.952–0.997) in training and 0.909 (0.807–1.000) in testing, with a Brier score of 0.143, a non-significant Hosmer–Lemeshow test (P = 0.367) and net benefit on decision curve analysis between 15% and 70% threshold probability.

The clinical translation. At the optimal Youden threshold (0.42), the integrated random forest yields on the test set a sensitivity of 83.3%, specificity of 90.9%, positive predictive value of 83.3%, negative predictive value of 90.9% and accuracy of 88.2%. Those percentages offer misleading comfort: converted back into counts, they mean that of 12 recurrences the model flagged 10 and missed 2, and of 22 non-recurrences it classified 20 correctly and 2 wrongly. The entire reported performance rests on four errors. Projecting these rates onto 1,000 patients at the same prevalence would give 292 recurrences detected, 58 missed and 59 false alarms — but the status of that calculation must be clear: it is an extrapolation of a threshold tuned on 12 events, not a measurement. The upper bound of the AUC confidence interval reaches 1.000, which is the statistical way of saying the sample cannot settle the question.

What is good

The anti-leakage discipline is explicit, detailed, and rare in this literature. Data leakage is the endemic failure mode of radiomics: when feature selection is run on the full dataset before the split, the test set has already been used to choose the variables, and the reported AUC is mechanically optimistic. Here the authors state in black and white that normalisation, resampling, ICC analysis, variance thresholding, F-test, LASSO and hyperparameter tuning are confined to the training set, and that the pipeline is then applied unchanged. They add a stability check across 1,000 bootstraps, variance inflation factors all below 5, and a Bonferroni correction declared in advance over six comparisons. On this specific point, the paper does better than most of what gets published in radiomics.

Segmentation is measured rather than asserted. Two radiologists segment independently, a third reviews, and agreement is quantified — mean Dice 0.85, range 0.72–0.94 — rather than declared satisfactory. The reproducibility filter that follows is not cosmetic: 38.5% of extracted features are discarded because they vary too much between contours. That is exactly the kind of number a reader needs, and one that many articles leave out.

The limitations are stated by the authors themselves, including the awkward one. The limitations section is long and candid. It says the internal test set "is limited", that the wide confidence intervals "reflect estimation instability", and above all that "the gap between the training AUC (0.975) and test AUC (0.909) suggests some degree of overfitting". The authors also flag that excluding 65.2% of screened patients introduces selection bias, that a 73.9% hepatitis B prevalence limits transfer to Western populations where alcohol and hepatitis C dominate, and that a seven-year inclusion window exposes the study to temporal drift in practice. None of this is buried.

What is less good

Twelve test events, nine models compared, and the winner reported as the model. This is the central problem. Three classifiers times three input sets makes nine models evaluated on the same 34-patient set; reporting the best of them amounts to selecting on the test set, which lets back in through the window the optimism the anti-leakage discipline had shut out at the door. And the gap is real for only one classifier: on the test set the support vector machine goes from 0.826 with radiomics alone to 0.830 integrated, and logistic regression from 0.830 to 0.830. The claim that "integrating clinical variables improves prediction" therefore rests entirely on the random forest, on 34 patients. Add an unfavourable events-per-variable ratio: 19 inputs for 49 training recurrences, or 2.6 events per variable where the classical rule of thumb asks for ten.

No external validation, and a split that tests none of what matters. The test set is a random draw from the same centre: same two scanners, same interventional surgeon, same adjudicating radiologist, same predominantly male and HBV-positive population. None of the factors that make radiomics models fail in the real world — a change of machine, of acquisition protocol, of operator, of epidemiology — is put to the test. The authors report having checked stability by vendor subgroup and suggest ComBat harmonisation for the future, but concede that normalisation and resampling "may not be sufficient to eliminate all scanner-related radiomics differences". This is population bias and distribution shift in their most classical form, and they remain untouched.

Nothing is reproducible, and the claimed comparator was never computed. Extraction is done on a proprietary platform, the "United Imaging Intelligent Scientific Research Platform System V1.0"; one co-author is affiliated with the Beijing United Imaging Intelligent Medical Technology Research Institute, that is, with the vendor of that tool. No code, no weights, no dataset is released — the availability statement points to "the corresponding author" — and the names of the 16 final features appear only in a supplementary table. A radiomics model whose extraction software and exact variable list are both unknown can be neither replicated nor audited. Finally, the discussion asserts "superior discriminative ability" over the CLIP and BCLC scores: no AUC was computed for CLIP or BCLC, and no comparison against a radiologist was run. Two minor numerical inconsistencies — the clinical AUCs in the abstract versus Table 5, and the random forest metrics at the default threshold versus at threshold 0.42 — also remain unreconciled in the text.

What it changes

For the research community. The pipeline-confinement protocol described here deserves to be copied: it is explicit, checkable, and cheap. But the paper mainly illustrates that upstream rigour does not compensate for a 34-patient test set. The real bottleneck in liver radiomics is not feature selection, it is multicentre external validation, and no one gets around it. Worth noting too, for reading the literature: "AI model" here means LASSO plus random forest, with no deep learning. The label has become so broad that it no longer says anything about the method, and one has to go and read.

For clinicians. The model changes nothing today — single-centre, retrospective, externally unvalidated, unavailable. The reusable finding lies elsewhere, and it is independent of the model: a special tumour location multiplies one-year recurrence risk by 6.4, and an ablation margin under 5 mm doubles it. Those two observations converge on a simple, actionable mechanism — the difficulty of achieving an adequate margin next to the diaphragm, the gallbladder or the porta hepatis — which belongs to indication and technique, not to an algorithm. A clinician who took only that from the article would have taken the essential part.

For patients and the public. Two ideas. First: after radiofrequency ablation for early-stage hepatocellular carcinoma, recurrence within a year affects roughly one patient in three, because the treatment destroys the tumour but leaves in place the diseased liver that produced it. Second, more generally: predicting is not preventing. A model that correctly identified at-risk patients would only change their prognosis if we knew what to do with that information — watch more closely, treat differently, add an adjuvant — and if a trial had shown that this course improves outcomes. That trial does not exist, and an AUC figure, however high, does not substitute for it.