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Do not judge a photovoltaic defect-segmentation model by one overall score. Report overlap and error trade-offs for each defect class, show performance by defect size, and state the dataset, split, label definitions, threshold, and aggregation method. Rare, tiny masks can be overwhelmed by background pixels, so a model may look strong on average while missing the defects it is meant to find.
Why rare and small defects need a different evaluation
Pixel-level segmentation has an imbalance problem when defects occupy only a tiny fraction of an image. A model can predict background correctly across most pixels and still fail to mark a crack, spot, or dead cell. Overall accuracy—and a single average score without class-level context—can therefore give a misleading impression of usefulness.
The scale of that problem is visible in the MSPS dataset, a binary semantic-segmentation collection of monocrystalline silicon photovoltaic cell electroluminescence (EL) images. Its project contributors report a mean background-to-defect pixel ratio of 2020:1, corresponding to approximately 0.05% defect pixels. The figures describe MSPS, not photovoltaic inspection generally. Its defect masks have a reported mean footprint of 128 pixels², a median of 114 pixels², and a range of 1–821 pixels². At that scale, a few pixels of boundary error can materially change a mask’s overlap score.
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Size also matters in published results. A 2023 EL benchmark reported higher mean intersection over union (mIoU) for large image features than for the smaller defects it evaluated. A 2025 multi-class study likewise reported different results for feature and defect classes. These findings make a practical point: an aggregate metric can hide weakness on small or uncommon targets. Evaluation should make those cases visible rather than letting the majority class or large structures dominate.
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Define exactly what the model is segmenting
Before comparing models, specify the task and its labels. A score only has meaning relative to the target definition: whether the model predicts one defect mask, several defect types, individual defect instances, or anomalous regions. State whether non-defect features are labeled as classes or treated as background, and clarify which defect types are included.
- Binary semantic segmentation: each pixel is assigned to defect or background. MSPS is this kind of task and covers busbar breaks, black spots, and cracks in monocrystalline silicon cell EL images.
- Multi-class semantic segmentation: pixels are assigned to one of several defect or feature classes. The 2023 benchmark uses 24 labeled classes; its abstract reports benchmark metrics for a subset of five. A separate 2025 study evaluates a 29-class PV module EL dataset.
- Instance segmentation: the model identifies separate object instances as well as their masks. The 2026 benchmark on UCF EL Defect evaluates this task, so its scores should not be treated as semantic-segmentation scores.
- Anomaly segmentation: the model marks unusual regions without necessarily assigning them to the same predefined defect taxonomy. If used, explain how predicted anomalies are matched to reference labels before reporting metrics.
Use the dataset’s precise label names and definitions. If a benchmark distinguishes a defect from a feature, do not combine the classes or call both “defects” without explaining the choice. Report whether labels are mutually exclusive, how ambiguous pixels are handled, and whether the model is evaluated on full images or crops.
Choose metrics that reveal both overlap and missed defects
Use at least one overlap measure—IoU or Dice/F1—alongside precision and recall. They answer different questions. Overlap measures how closely the predicted mask matches the reference mask. Precision indicates how much of the predicted defect area is actually labeled as defect; recall indicates how much of the reference defect area the model found. Reporting them together helps distinguish false-positive area from missed defects.
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| Metric | What it measures | What to watch for with rare or tiny targets |
|---|---|---|
| Intersection over union (IoU) | Intersection of predicted and reference masks divided by their union. | A strict overlap measure; a small displacement can sharply reduce the score for a tiny mask. |
| Dice / F1 | Twice the intersection divided by the sum of predicted and reference mask sizes. | Also measures overlap, but its values are not interchangeable with IoU. Name the metric and its averaging method. |
| Precision | The share of predicted defect pixels or instances that are correct. | Low precision indicates false-positive predictions; clarify whether the unit is pixels or instances. |
| Recall | The share of reference defect pixels or instances that are detected. | High recall does not prove accurate localization. A broad mask can cover a defect while also including much incorrect area. |
| Pixel accuracy | The share of all evaluated pixels assigned the correct label. | Can appear high when background dominates, even if the model misses defects. |
| mAP at a specified IoU threshold | Average precision under an instance-detection evaluation convention and stated overlap threshold. | Keep it with the instance-segmentation task and report the threshold; do not compare directly with semantic mIoU. |
The distinction between recall and localization is not merely theoretical. In the 2023 EL benchmark, a reported DeepLabv3+ result with custom class weights achieved 86% recall for cracks while reporting 25% IoU for cracks. These are results for that model and dataset, not a general expected performance level. Their combination illustrates why recall alone cannot establish that predicted boundaries or covered regions are accurate.
For semantic segmentation, state whether precision and recall are computed over pixels, images, or class instances. For instance segmentation, state the matching rules and whether metrics count objects or pixels. A percentage without that definition can be difficult to interpret or reproduce.
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Report class-level results instead of hiding rare classes in an average
Show each defect class separately, including the rarest classes. For every class, report IoU or Dice and precision and recall, alongside support: the number of test images containing that class and, where applicable, the number of annotated instances or pixels. Support helps readers judge how much evidence lies behind a score. If a class appears in only a few test images, the result is less informative than the same score supported by many examples.
Explain how you aggregate classes. A macro average gives each class equal weight; a frequency-weighted average gives more weight to classes with more pixels or examples. A micro average pools counts before calculating a metric and may be dominated by common classes. None is self-explanatory: label the method, retain the per-class table, and avoid presenting one average as if it represented every class equally.
The 2025 multi-class study reports mean IoU of 0.663 for feature classes and 0.326 across defect classes. It also reports a 0.129 IoU improvement for rare dead-cell defects in its comparison. Preserve the study’s task and comparison context when quoting these results; they are not a universal performance target or a direct comparison with other datasets. They show why the aggregate should be accompanied by class-level figures.
For binary tasks, include both the defect result and the background result if reporting class averages, but keep the defect-focused metrics prominent. A background score can dominate the narrative when most pixels are background. Make clear whether the reported “mean” includes background and whether absent classes in an image are included, excluded, or treated by a stated convention.
Break results down by defect size
A model that handles large masks may fail on tiny ones. Add a size-stratified report so that small-target behavior is observable rather than inferred from the overall score. Define bins using the dataset and task—for example, by reference-mask pixel area or another explicitly stated measure—and report the number of cases in each bin. There is no universal threshold established by the cited benchmarks, so do not present a particular pixel cutoff as a standard.
- Define size from the ground-truth mask, not the model prediction, so a missed defect does not disappear from the size analysis.
- Give the bin boundaries and the number of images or instances per bin.
- Report the same overlap and error measures within each bin where support permits.
- Show representative examples of tiny, low-contrast, irregular, and correctly detected masks, including misses and false alarms.
- If contour fidelity matters for the inspection decision, add a boundary-sensitive measure and define it. The cited material does not establish one preferred boundary metric for all PV tasks.
MSPS project contributors describe minute targets, low contrast, varied sizes, irregular boundaries, and strong foreground-background imbalance. Such properties affect interpretation: one-pixel shifts matter disproportionately for a 1-pixel² or similarly tiny region, while the same shift has less effect on a large area. A size-stratified table and image examples make that difference visible.
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Document the dataset and split, including whether the split is official or custom. Keep the test set separate from every decision that tunes the model, including threshold selection and hyperparameter changes. If images are cropped, ensure that related crops do not end up on both sides of the split. Where images may share a source cell, module, acquisition session, or other relationship, describe how that relationship was handled; otherwise, apparent test performance may reflect similarity between training and test data rather than generalization.
This grouping advice is methodological guidance, not a universal split rule established by the cited dataset descriptions. State the actual grouping method used rather than implying that one is mandated. Include the number of images in each split and enough information to identify the acquisition domain, modality, cell or module type, and labeling scheme.
MSPS provides a concrete reference point: its 2026 dataset record describes 1,500 images at 640 × 590 pixels, with 1,000 training images and 500 test images. The project describes expert annotations: two experts annotated each image and a third reviewed disagreements. These details are specific to that dataset and should not be assumed for other benchmarks.
Compare models on the same held-out examples, with the same label mapping, preprocessing, evaluation code, and operating threshold selection procedure. If a method uses more labeled data, unlabeled data, or different training labels, state that difference. Report whether the comparison uses a fixed test set and whether reported values are from one run or multiple runs.
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Set and report the operating threshold
Segmentation models often produce probabilities or scores that must be converted into masks. The threshold used for that conversion can change the trade-off between false positives and missed defects. State the threshold and how it was chosen. If it was selected to optimize a validation metric, name that metric and confirm that the test set was not used to choose it.
For deployment-oriented evaluation, a single threshold may not capture the decision-makers’ needs. Consider showing how precision and recall change across thresholds, or report results at a threshold chosen for a clearly stated operating objective. Do not select a threshold after inspecting test outcomes and then present the resulting score as an unbiased test result.
State any post-processing that changes masks, such as removing small connected regions or filling gaps. Such steps may reduce false alarms or erase small real defects. Compare models using consistent post-processing rules, and disclose any class-specific rules.
Test imbalance treatments without changing the rules of the comparison
Class weighting, resampling, and semi-supervised learning can be evaluated as ways to address sparse examples or foreground-background imbalance. The 2023 benchmark evaluates class-weight configurations; the 2025 multi-class work uses custom class weights; and PV-S3 evaluates a semi-supervised semantic-segmentation approach with a proposed semi-cross-entropy loss. These approaches are not interchangeable, and their results should be interpreted within each study’s dataset, labels, and comparison design.
To determine whether an imbalance treatment helps, hold the split, evaluation code, thresholds, and reporting rules constant. Show the effect per rare class as well as the aggregate: a change that improves a common class can conceal a regression on a rare defect. State the labeled and unlabeled data available to each method, and do not imply equal supervision if the training data differ.
PV-S3’s project authors report an absolute 9.7 percentage-point mIoU improvement on UCF-EL using 20% labeled samples, compared with a supervised comparison using 100% labeled samples. This is the authors’ reported comparison on that dataset, not a cross-study guarantee or proof that semi-supervised methods will outperform supervised methods in another setting.
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Scores from different datasets should not be arranged into a single leaderboard unless the task, labels, metric definitions, and evaluation rules genuinely align. For orientation, the cited PV work spans binary semantic segmentation, multi-class semantic segmentation, semi-supervised semantic segmentation, and instance segmentation:
| Work or dataset | Task and scope | Reported details | Interpretation limit |
|---|---|---|---|
| MSPS | Binary semantic segmentation of monocrystalline silicon cell EL defects, including busbar breaks, black spots, and cracks. | 1,500 images at 640 × 590 pixels; 1,000 training and 500 test images. Mean background-to-defect pixel ratio 2020:1; approximately 0.05% defect pixels. | Dataset-specific properties; not a universal PV class balance or a multi-class benchmark. |
| 2023 EL benchmark | Semantic segmentation over 24 labeled defect and feature classes. | 593 cell images and 50 test images; its abstract reports metrics for a subset of five classes. A reported DeepLabv3+ custom-weight result includes 25% IoU and 86% recall for cracks. | Results apply to the reported model, classes, and dataset; feature and defect scores are not equivalent targets. |
| 2025 multi-class study | Multi-class segmentation on a 29-class PV module EL dataset. | Evaluates six U-Net/SegNet architectures with VGG16, MobileNet, or ResNet50 encoders and custom class weights. Reports mIoU 0.663 for feature classes and 0.326 across defect classes; a rare dead-cell IoU improvement of 0.129. | Keep the task and comparison context attached to the figures; do not treat them as a universal benchmark threshold. |
| PV-S3 | Semi-supervised semantic segmentation using labeled and unlabeled data. | Authors report an absolute 9.7 percentage-point mIoU improvement on UCF-EL with 20% labeled samples versus a supervised comparison using 100% labeled samples. | Authors’ reported comparison, not a result guaranteed on other datasets or labeling regimes. |
| 2026 UCF EL Defect benchmark | Instance segmentation, comparing Mask R-CNN, ConvNeXt, ConvNeXt-V2, and Mask2Former. | ConvNeXt-V2 reports segmentation mAP at IoU 0.50 of 0.602 and segmentation mIoU of 0.650. | Instance-segmentation results are not directly interchangeable with semantic-segmentation scores. |
Even identical metric names may conceal differences in implementation or aggregation. When reporting mIoU, state which classes are included, how missing classes are handled, and whether the average is macro, weighted, or computed by another convention. For mAP, specify the evaluation threshold and matching protocol. The 2026 instance-segmentation figures are useful in their own task context, but not as a direct ranking against semantic-segmentation results.
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A score from one run may reflect a particular random seed, split, or training configuration. Where feasible, report variability across runs or confidence intervals, and explain how they were calculated. If only one run is available, say so. The cited benchmark summaries do not establish a shared statistical protocol, so describe your own method rather than suggesting it is standard across PV segmentation.
For an operational comparison, report false alarms and misses in units that matter to the inspection workflow, such as false-positive images or missed annotated instances, in addition to pixel measures. These views are complementary: a few scattered erroneous pixels can reduce precision without creating a practical alarm, while one missed small defect can be important even if its pixel count barely changes a dataset-wide metric.
If throughput is relevant, report the hardware, input resolution, batch size, and whether timing includes preprocessing and post-processing. The MSPS project reports throughput measured on an NVIDIA RTX 3090 Ti in its benchmark context. That identifies the conditions for its report; it does not establish that this GPU is required to reproduce the dataset or is the right hardware for every deployment.
A practical evaluation report checklist
- Describe the target: task type, image modality, label definitions, included classes, and treatment of ambiguous regions.
- Identify the data: dataset version or record, acquisition context, image count, resolution, split, and any grouping rule used to avoid related samples crossing splits.
- Show support: images, instances, and where useful pixel counts per class and per size bin.
- Report complementary metrics: per-class IoU or Dice plus precision and recall, with units and aggregation method stated.
- Expose small-target behavior: size bins based on reference masks, representative examples, and boundary-sensitive measures only when their definitions and purpose are clear.
- Document decision settings: probability threshold, threshold-selection procedure, and all post-processing.
- Make comparisons fair: use the same held-out data and evaluation rules, describe differences in labels or supervision, and separate semantic from instance segmentation.
- Bound the conclusion: name the tested cell or module type and imaging conditions, and report run variability or explain its absence.
A result is most useful when a reader can tell which defects were evaluated, how many examples supported each class score, how well small masks were localized, and what false-positive/missed-defect trade-off was measured. If those facts are absent, an impressive overall average is not enough to establish that a model can reliably detect rare photovoltaic defects.
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