médical IA

Polyp detection in colonoscopy: trained on curated clips, models collapse on full procedures

Published on August 20, 2026 · 13 min read

Six researchers at the xAILab in Bamberg retrain four real-time object detectors — Faster R-CNN, YOLOv8, YOLOv11 and RT-DETR — on colonoscopy datasets cropped around polyps, then test them on 60 complete, unedited procedures. The drop is stark: YOLOv11 falls from mAP50 of 0.724 on the SUN benchmark to 0.164 on full procedures, with frame-level sensitivity down to 0.240 at a matched false-alert rate. The asymmetry is the real finding: in the other direction, models trained on full procedures retain mAP50 of 0.705 to 0.717 when transferred back to SUN — it is the curated benchmarks that prepare a model for nothing, not the real data that would be too hard.

The context

Colonoscopy is the reference examination for preventing colorectal cancer: precancerous lesions — polyps — are located and removed in the same procedure. The problem is old and well documented: miss rates reach 27% in the series cited by the authors. A polyp appears for a few seconds, behind a fold, in a specular highlight or motion blur, and the endoscopist misses it.

Hence CADe systems (computer-aided detection): an object detector runs in real time on the video stream and draws boxes around suspected polyps on screen, as a safety net. Several products are on the market — Medtronic's GI Genius, Olympus's EndoAID — and randomised trials have shown gains in adenoma detection rate. Yet broad deployment remains slow, and the gap between published performance and behaviour in the examination room remains poorly explained.

This paper's hypothesis concerns the data, not the architectures. Public colonoscopy datasets are almost all lesion-centric: clips or images have been cropped around the polyps. But a real examination is twenty to thirty minutes, the overwhelming majority of which contains no polyp at all — healthy mucosa, instruments, wash fluid, empty stretches during insertion and withdrawal. Training and evaluating a detector on curated clips means never showing it what it will have to say no to for 95% of its working life.

The method

The protocol. The authors establish TRUE-Colon, a standardised evaluation protocol on REAL-Colon (Biffi et al., Scientific Data, 2024): 60 complete, unedited colonoscopies from four centres, with strict patient-level separation and a 10/2/3 video split per centre — 40 training videos, 8 validation, 12 test. The training set holds 1,706,635 frames of which 86.5% contain no annotated polyp; the test set, 572,085 frames of which 85.7% are negative.

Against it, two curated benchmarks. SUN: video clips, 70 positive and 7 negative for training, 76% negative frames at test — curated at clip level. PICCOLO (Basque Biobank): still images, 2,203 for training of which 20 are negative, and a test set of 333 images containing a single negative image. On such a set, measuring a false-alert rate is mathematically meaningless — and yet this is the standard format of part of the literature.

The four characteristics measured. This is the methodological contribution. Beyond localisation accuracy (mAP50, mean average precision when the predicted box overlaps at least 50% of the reference box), TRUE-Colon quantifies three things curated benchmarks cannot measure: false-alert burden (proportion of polyp-free frames that nonetheless trigger an alert), detection latency (number of frames between lesion onset and first valid detection) and temporal reliability (a lesion counts as persistent if detected in at least half the frames where it is visible — a box that flickers once does not have the same clinical value as one that holds).

The models. Four real-time detectors in their default recipes, 640 × 640 input, 100 epochs with early stopping, three random seeds: Faster R-CNN and RT-DETR on one side (the latter is a transformer, an attention-based architecture, more data-hungry), YOLOv8-M and YOLOv11-M on the other (convolutional, faster).

The matched operating point. This is the paper's most important move. Comparing detectors at the same confidence threshold — typically 0.2 — is misleading, because each architecture calibrates its scores differently: at the same nominal threshold, one fires twice as often as another. The authors therefore pick a model-specific threshold, written tau-star, such that the frame-level false-alert rate falls in a 4–5% band. Sensitivities are then compared at equal alert burden, which is the only clinically readable comparison.

The results

On curated benchmarks, all is well. SUN to SUN: mAP50 from 0.689 to 0.738 depending on architecture, frame-level sensitivity around 0.73 at a 4–5% false-alert rate. PICCOLO to PICCOLO: YOLOv11 reaches 0.770. This is the picture standard literature produces.

On full procedures, collapse. The same models trained on SUN and tested on REAL-Colon at matched false-alert burden: YOLOv11 falls from 0.724 to 0.164 mAP50, sensitivity 0.240; RT-DETR from 0.689 to 0.225 (sensitivity 0.310); Faster R-CNN to 0.220 (0.290). Trained on PICCOLO it is worse: YOLOv11 at 0.059, and RT-DETR at 0.012 with sensitivity 0.007 — the model detects essentially nothing.

And the asymmetry. In the other direction, models trained on the 40 full procedures and tested on SUN retain mAP50 of 0.705 (YOLOv11), 0.714 (YOLOv8) and 0.717 (RT-DETR) — on par with, or above, what the same architectures achieve when trained on SUN itself. On PICCOLO the transfer drops to 0.554–0.645, still far above the reverse transfer. In other words: full video contains the information in curated clips; the converse is false.

Under realistic conditions. Trained and tested on REAL-Colon at a fixed threshold of 0.2, RT-DETR appears dominant (mAP50 0.488; sensitivity 0.720) — but at an 8.2% false-alert rate against 1.7–2.0% for the YOLO models. Once operating points are matched around 4.3–4.6%, the gap largely closes: RT-DETR 0.651 sensitivity, YOLOv8 0.605, YOLOv11 0.573, Faster R-CNN 0.463. RT-DETR keeps an edge on latency (38.3 frames on average to first detection, against 46.8 for YOLOv8 and 63.9 for Faster R-CNN) and on persistence (17.3 of 21 lesions detected persistently, against 11.7 for Faster R-CNN), but the authors themselves state that these lesion-level gaps fall within seed variance on 21 test lesions and should be read as trends.

Clinical translation. A 4.3% per-frame false-alert rate sounds negligible. On the REAL-Colon test set that means 489,979 negative frames spread over 12 examinations — roughly 40,800 polyp-free frames per examination, close to 23 minutes at 30 frames per second. At 4.3%, that is on the order of 1,750 spurious alert frames per examination, close to a cumulative minute during which a box lights up on healthy mucosa. This calculation is our extrapolation from the paper's figures, and the authors are explicit about its limit: a per-frame measure does not distinguish one continuous thirty-second alert from a thousand isolated interruptions, though the two scenarios are nothing alike from the endoscopist's point of view.

A benchmark point. In an appendix the authors set their figures beside those published by Troya et al. on commercial systems: GI Genius v1 at 0.506 sensitivity for 2.8% false alerts, GI Genius v2 at 0.679 for 3.8%, EndoAID A at 0.656 for 2.5%. The open detectors evaluated here reach 0.60–0.72 sensitivity but at roughly 4.5% false alerts. Contextual comparison only — different dataset and pipeline — but it locates the remaining gap: it lies in false-positive control, not in raw sensitivity.

What is good

The protocol measures what benchmarks cannot. False-alert burden, latency and persistence are three quantities that decide whether a CADe is clinically usable, and none of the three is computable on a set of still images. The authors demonstrate this literally by showing that PICCOLO's test split contains a single negative image. This is a structural contribution, not one more architecture.

Matching operating points defuses a recurring trap. Comparing architectures at identical confidence thresholds conflates model quality with score calibration. The paper quantifies the effect: at threshold 0.2, RT-DETR looks far superior; at equal alert burden, its sensitivity gap with YOLOv8 shrinks from 21 points to under 5. Many published rankings in this field would not survive that normalisation.

Transparency about limitations is unusually precise. The authors flag six restrictions themselves, two of which directly weaken their own conclusions: tau-star is selected on the test split, and the curated-versus-procedure contrast confounds data realism with scale and negative-frame prevalence. Code is published on GitHub, REAL-Colon is CC BY 4.0, funding is public (Hightech Agenda Bayern), no competing interests declared.

What is less good

The comparison threshold is chosen on the test set. The authors say so: tau-star is set post hoc on the evaluation data to equalise false-alert rates. That is methodologically defensible for a controlled comparison between architectures, but it remains a form of optimism — a deployed system would have to fix its operating point on a separate validation set, and would then see its rates drift. The sensitivities reported at tau-star are therefore ceilings, not field predictions.

The lesion-level evidence rests on 21 lesions from a single cohort. Latency and persistence metrics — the ones carrying the architecture comparison — are computed on twenty-one lesions from 12 examinations. The authors note that the observed gaps fall within seed variance. The robust conclusion of the paper is the transfer asymmetry, not the RT-DETR-versus-YOLO ranking, and the temptation to read the second as a result should be resisted.

The underlying failure mode is not isolated. What happens can be named precisely: models trained on curated clips never learned to reject non-polyp content, for want of exposure — a classic distribution bias, compounded by a misleading metric (an mAP computed on almost always positive frames says nothing about alert burden) and a biased comparator (the fixed threshold). But the paper does not separate the share due to negative-frame prevalence from the share due to visual domain: a control training on REAL-Colon's lesion-bearing frames alone would have settled it. The authors acknowledge this and did not run it. They also report near-zero performance on small polyps — precisely those missed in practice.

What it changes

For the research community. The message is direct: publishing an mAP on SUN or PICCOLO says nothing about a detector's usability, and the asymmetry quantified here removes the cost excuse. Since training on full video does not degrade performance on curated benchmarks — it matches or exceeds it — there is no longer a reason to keep training on clips. With the protocol published alongside its code, it can be adopted directly as a minimum evaluation grid. The natural next step, which the authors point to, is temporal modelling: their four detectors are memoryless, processing each frame in isolation, while consistency between consecutive frames is the most obvious signal to exploit for reducing both latency and erratic alerts.

For clinicians. Nothing changes in tomorrow's practice: these are research detectors, not CE-marked or FDA-cleared devices. But the paper supplies a vocabulary for questioning a CADe vendor: what data was the model trained on — curated clips or full procedures? Is the stated false-alert rate measured on whole procedures, and at what operating point? How many alerts per examination, not per frame? Those three questions discriminate, and the paper shows they are not rhetorical.

For patients and the public. The claim "an AI detects polyps with 77% accuracy" means close to nothing until one knows which frames the number was computed on. This work shows that between a test set built around lesions and a real colonoscopy, the same model can go from three quarters of correct detections to under a quarter. This is not an argument against AI in endoscopy — commercial systems have been evaluated under real conditions — but a reminder that the performance of a medical model does not exist in the abstract: it exists only relative to the data on which it was measured.