PruDensNet: a parameter efficient depthwise separable CNN for MRI-based brain tumor classification
Frontiers in Medicine (2026) · 1 comment
doi 10.3389/fmed.2026.1743015 PMID 42245956 issn 2296-858X
Correspondence · 1 comment
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The patient-information statements contradict each other. The authors say that no patient identifiers were available, so they could not distinguish patients individually. Immediately afterward, however, they claim that duplicate patient removal was performed. If patient identities were unavailable, it is unclear how duplicate patients could have been identified and removed.
The supposedly “held-out” test set appears to have been checked throughout training. The methods explicitly state that the predefined Testing folder was held out and was not used for model selection or early stopping. But Figure 12 plots test accuracy and test loss for every training epoch. At minimum, this makes the meaning of “held-out test set” unclear, because the test performance was apparently monitored repeatedly during model development.
The main model-comparison accuracy appears to use the validation result, not the test result.Table 2 reports PruDensNet accuracy as 0.9727. But Table 5 shows that 0.9727 is the validation accuracy, whereas Table 6 gives the actual test accuracy as 0.9605. Despite this, Figure 7 describes the comparison as being under the same “test setting.” This is one of the most important inconsistencies because it affects the claim that PruDensNet outperforms all baselines on the test set.
The confusion-matrix explanation says the opposite of what a confusion matrix means. The Figure 8 caption correctly says that most correct predictions lie along the diagonal . But the following paragraph says that predictions lying “above or below the diagonal” indicates good class-wise accuracy. Those statements directly contradict each other.
The paper says glioma has “perfect precision,” but the tables show that it does not. The discussion states that glioma achieves perfect precision. However, precision is 0.9688 on validation and 0.9844 on test, neither of which is perfect.
Figure 4 disagrees with the written MixUp method. Section 3.3 states that MixUp uses α = 0.3. However, the Figure 4 diagram on page 7 visibly labels MixUp as α = 0 . These cannot both describe the same implementation.
Figure 5 does not match the architecture described in the text. The text clearly specifies three SepBlocks—F1=128, F2=320, F3=640—followed by GAP, one Dense(256) layer, dropout and softmax. But the architecture diagram on page 8 visibly contains duplicated F2=320 and Dense 256 + GELU blocks and an unclear processing path. Therefore, it is difficult to know which architecture was actually implemented.
The “Parameter Target Padding” argument is methodologically questionable. The authors add trainable parameters and then multiply them by zero , meaning they have no effect on the model output. Nevertheless, the paper claims this “equalizes capacity.” Adding inactive parameters can equalize the reported parameter count, but it does not actually equalize functional model capacity. Therefore, the claim that this isolates architecture from capacity is much stronger than the procedure supports.
The reported memory results contradict the lightweight-memory narrative.PruDensNet has only 1.46M parameters, but Table 4 reports 4,690.53 MB peak GPU memory , compared with only 177 MB for MobileNetV4, 194 MB for EfficientNetV2 and roughly 292–565 MB for several much larger models. Yet immediately afterward the paper describes the experiment as operating under “tight parameter and memory budgets.” Based on its own table, PruDensNet actually has by far the highest reported GPU-memory use.
The latency claim also needs qualification.PruDensNet reports 12.031 ms inference latency, while MobileNetV4 is 4.623 ms, ConvNeXt V2 Tiny 8.339 ms, EfficientNetV2 B0 8.902 ms and RegNetY 11.472 ms. So the small parameter count does not translate into the best latency or memory efficiency in the paper's own hardware benchmark.
The authors promise repeated-seed results but do not appear to report them. The methodology says results across multiple random seeds are presented as mean ± standard deviation for accuracy and macro-F1. However, the main results tables report single accuracy values rather than the promised mean ± SD results. The PDF does not provide a clear seed-wise robustness table.
Figure 7 and Figure 10 appear to be essentially the same accuracy-comparison figure. Figure 7 on page 12 and Figure 10 on page 14 show the same ordered model-accuracy comparison and carry almost identical captions. This looks like unnecessary duplication or a figure-management error.
The duplicate-removal method is described more strongly than it actually operates. The paper calls it “near-duplicate removal,” but it computes a 64-bit a Hash and removes an image only when the generated key is already present within the same class. This is essentially a zero-distance hash match rather than a general perceptual near-duplicate search, and cross-class duplicates would not necessarily be detected.
The Data Availability Statement is unusually vague for a reproducibility-focused paper. It merely says that original contributions are contained in the article/supplementary material and that inquiries can be directed to the corresponding author. Yet the methodology repeatedly refers to a public Brain Tumor MRI dataset and a detailed Kaggle-style pipeline. The paper does not provide a clear dataset URL or code repository in this statement.
There are also citation/source mismatches. For example, the text attributes the development of ResNet-RS to reference [16], but reference [16] is titled “Impact of light and shadow on robustness of deep neural networks,” not the ResNet-RS architecture paper. Likewise, LeViT (128S) and TinyViT are both associated with reference [37] in the text, while reference [37] is a TinyViT application paper and is not the original LeViT source.