W1. Limited novelty: the contribution is an assembly of existing components
The proposed method does not introduce a new architectural principle, a new optimization objective, or a theoretical result.
Multi-center / mixture prototypes are a well-established idea: Prototypical Networks (Snell et al., 2017) use one center per class, and mixture-of-prototypes approaches (e.g., Infinite Mixture Prototypes, Allen et al., 2019; and numerous multi-prototype metric-learning works) already model heterogeneous class structures with several centers and max-similarity aggregation. The paper's "fundamental distinction between multi-center and single-center prototypes" (§3.4) is therefore not new to the literature.
The intra-class compactness loss (Eq. 11) and inter-class hinge separation loss (Eq. 12) are standard metric-learning regularizers (center-loss / contrastive / NCA-style terms); the entropy-weighted EMA is a stabilization heuristic; UDC and the self-regulated consistency loss (Eqs. 3, 16) are inherited from MMLoP / PromptSRC.
The genuinely novel content is the combination of these components inside a frozen-CLIP prompt pipeline for one narrow domain. No generalizable insight about prompt learning, prototype learning, or representation learning is extracted that would transfer to other VLM adaptation tasks. For an ICLR submission, this level of contribution reads as a domain-specific engineering integration rather than a representation-learning advance.
W2. Private, tiny dataset; the "state-of-the-art" claim is not statistically supported
Test set is too small for the reported gaps. The test split contains only 174 samples, and the smallest classes are extremely thin: Suspension 18 test samples, Air Gap 25, Surface 26 (Table 4). On 18 test samples, a single misclassification moves per-class recall by roughly 5.6 percentage points. The reported improvements over MMLoP (OA 97.7 → 98.9, +1.2) and over MMA (98.3 → 98.9, +0.6) are well within the sampling noise of such a split. The paper reports a single run with no mean ± standard deviation over multiple random seeds, no confidence intervals, and no paired significance test (e.g., McNemar's test or bootstrap on OA). As written, the claim that MCP-MMLoP "achieves state-of-the-art performance" cannot be distinguished from run-to-run variance.
The dataset is withheld and the SOTA claim is unverifiable. The authors state in §5 that no public PRPD benchmark exists and that all experiments are run on their own self-collected data; the dataset itself is not released. Reviewers and the community cannot reproduce the 98.9% OA, the silhouette scores, or the baseline numbers. A SOTA claim on a private, non-reproducible dataset is, at best, a claim about this particular split.
No generalization or domain-shift evaluation. All results come from one random 8:1:1 stratified split of one laboratory dataset. There is no cross-validation, no evaluation across apparatus types (cable, GIS, transformer, rotating machine), voltage levels, measurement noise conditions, or collecting laboratories. §1 itself emphasizes that PRPD patterns vary under "variable practical measurement conditions," yet the paper never tests robustness to those conditions.
The main comparison excludes the domain-specific baselines the paper itself cites. §2.1 reviews CNN, CNN-LSTM, MobileNet, capsule-network, data-augmentation, and metric-learning PD methods (Peng et al., 2019; Liu et al., 2021; Sun et al., 2021; Jia et al., 2026b; Li et al., 2025; Yan et al., 2025), but Table 1 compares only VLM prompt/LoRA methods. Claiming PRPD state-of-the-art without comparing against the established CNN/Transformer/metric-learning PRPD literature is an apples-to-oranges comparison and leaves the central empirical question — whether a VLM prompt pipeline actually beats specialized PD classifiers — unanswered.
W3. The core ablation is missing, and the reported ablation is internally contradictory
The central claim — multiple sub-prototypes versus a single prototype — is never tested. The method's headline contribution is assigning K = 3 sub-prototypes per class, but Table 2 contains no K = 1 single-center prototype baseline (the classic Prototypical Network setup), and Figure 5(a) only sweeps K upward without reporting a K = 1 result. Consequently, the paper does not isolate the very effect that justifies the MCP module. The reported gain could equally come from the EMA update, the regularizers, or the prototype-path score, none of which is separated.
The listed ablation variants appear mis-specified and cannot support the claimed attribution. §4.4 describes "MMLoP with only L_intra" and "MMLoP with only L_inter," yet Table 2 shows both variants dropping OA from 97.7 to 95.4 — below the MMLoP baseline — meaning the regularizers in isolation are harmful. The paper then attributes the full-model improvement to "complementarity between intra-class attraction and inter-class separation," but the factorial design omits the decisive cells: prototype path without either regularizer; prototype path + L_intra only; prototype path + L_inter only; and MCP with uniform (non-entropy-weighted) EMA. Without these cells, the ablation cannot assign credit to prototype count, EMA weighting, or the two losses.
Hyperparameter selection on an undersized validation set. K = 3, λ_intra = λ_inter = 5.0, β = 0.5, and margin m = 0.2 are presented as fixed best settings (§4.6, Table 5), but the validation set contains only 167 samples and the paper does not state that the final numbers were frozen before inspecting the 174-sample test set. Sweeping K and the regularization weights on this small validation set, and reporting the chosen peak on the same test split, risks evaluation-set selection bias. β and m are never ablated at all.
W4. The method description is not closed-loop: dimension bookkeeping, gradient flow, and several equations are inconsistent
Eq. (1) dimension inconsistency. The prompt matrices are written P_v^(l) = U^(l) V_v^(l) with U^(l) ∈ R^{T×r}, V_v^(l) ∈ R^{r×d_v}; the text then states that U is a shared up-projection with T equal to the visual prompt length and that "the visual branch reuses it after dimensional adaptation." The relationships among prompt length T, text prompt length T_t, rank r, d_v, and d_t are never derived, and a rank-1 factorization sharing one U across two modalities with different prompt lengths needs an explicit projection definition. The notation in §3.2 should be reconciled with Figure 2 and Table 5 (r = 1, T = V = 4, L = 9).
Prototype gradient path is unclear and likely conflicts with EMA. Prototypes are updated by EMA (Eq. 10) rather than backpropagation, yet L_intra (Eq. 11) and L_inter (Eq. 12) are functions of prototype positions. Algorithm 1 step 12 updates the low-rank factors by minimizing the full objective, while step 13 EMA-updates the prototypes. The paper does not state whether p_{c,k} receive gradients from L_intra/L_inter, whether they are detached from the autograd graph, or how the EMA overwrite reconciles with any gradient step on the prototype vectors. A gradient-flow statement (which tensors are trainable, which are stop-gradient) and a revised parameter table are required; as written, the optimization mechanism is not reproducible from the manuscript.
Eq. (10) shrinks prototype norms and breaks cosine geometry. The EMA update p ← η p + (1 − η) \bar w_n f_n multiplies the feature by the per-sample scalar weight \bar w_n ∈ [0, 1). Because \bar w_n is normalized across classes (Σ_c w_c = 1) and then aggregated through the soft label, it systematically down-scales the incoming feature, progressively shrinking prototype norms. Since the prototype-path score is cosine similarity (Eqs. 6–7), norm drift changes the effective geometry; the update also lacks batch-level averaging over the matched samples. A normalized EMA (or explicit norm control and batch aggregation) should be specified and ablated.
Eq. (9) entropy is not a valid class-uncertainty measure. The class marginal is \bar p_c = (1/B) Σ_n q_{n,c}, and the paper defines \bar H_c = −\bar p_c log \bar p_c. This is a one-sided binary form that does not measure the dispersion of a class's predictions: a proper class-level uncertainty is either the binary entropy −\bar p_c log \bar p_c − (1 − \bar p_c) log(1 − \bar p_c), or the entropy of the per-sample C-class prediction distribution. The current scalar expression should be corrected and its weighting scheme justified.
Dual-path fusion mixes uncalibrated scores. ℓ_c = s_c + β g_c adds a visual–text prompt-path cosine similarity and a visual–prototype cosine similarity directly, without per-path normalization, calibration, or a learned weighting; β = 0.5 is fixed and never ablated. The two scores may occupy different scales, and the paper does not report score statistics per path. UDC (Eq. 3) corrects only the text embeddings; the analogous drift in the prompted visual feature \tilde f_p is left unaddressed.
L_inter scales quadratically and its margin is unjustified. The hinge term sums over all cross-class prototype pairs, i.e., C(C − 1)K²/2 pairs (135 pairs at C = 6, K = 3), growing quadratically in both class and prototype counts. The margin m = 0.2 is asserted without physical or empirical justification, and no sensitivity analysis for m is provided.
W5. The efficiency claim has no computational measurements
The abstract and §1 position the paper around an "efficiency–accuracy trade-off," and Appendix C.3 states that the prototype module adds "only one matrix multiplication" with "negligible extra parameter and computational overhead." Table 1 reports trainable parameter counts only; there are no inference latency, FLOPs, peak memory, or throughput numbers against any baseline. Parameter count alone does not establish computational efficiency — the prototype-path max aggregation over K centers, the EMA update, and the two regularizers all carry runtime cost that should be measured and reported.
W6. Few-shot evidence is incomplete and robustness is untested
Figure 4 is described only as MCP-MMLoP's own OA/F1 curve across 4, 8, 16, 32 shots; the paper does not report side-by-side few-shot performance for MMLoP, CoOp, MaPLe, or MMA under the same episodes, so the claimed few-shot advantage is not evidenced. The episode construction protocol (stratified sampling from the private training set? number of repeated episodes? mean and variance over episodes?) is absent.
Despite §1's emphasis on variable measurement conditions, there are no robustness experiments against noise level, amplitude scaling, phase-offset or missing-cycle corruption, label noise, or domain shift. The Normal class reaches 100.0% recall for nearly every baseline in Table 1, which raises the possibility that the model recognizes background-noise level rather than defect morphology; this shortcut should be explicitly analyzed.
W7. Reproducibility and open-science
The reproducibility statement releases source code only "upon paper acceptance," and the dataset is withheld. Reviewers therefore cannot verify the main table, the ablation, the t-SNE silhouette values, or the one-click baseline reproduction claimed in §Reproducibility Statement. For a result that rests on a private dataset and a small number of test samples, this substantially weakens the paper's evidentiary standing.
W8. Scope fit
The submission is a vertical power-engineering integration of frozen-CLIP prompting and prototype classification. It contributes no method that other representation-learning communities can reuse, which limits its fit to ICLR's broad representation-learning audience; the same material would be a better fit to a power-delivery / condition-monitoring venue.