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Withdrawn from ICLR 2027

Multi‑Center Prototype Enhanced Multimodal Low‑Rank Prompting for Phase-Resolved Partial Discharge Recognition

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Phase-Resolved Partial Discharge (PRPD) recognition aims to identify insulation defects using partial‑discharge patterns of power equipment. Existing methods suffer from significant intra-class morphological diversity, inter-class feature overlap, as well as the efficiency‑accuracy trade-off. To tackle these issues, we propose MCP-MMLoP, a dual-module framework consisting of a MMLoP module and a multi-center prototype (MCP) module. Specifically, the MMLoP module realizes parameter‑efficient model adaptation via multimodal low‑rank prompting to mitigate the efficiency‑accuracy trade‑off. Additionally, the MCP module equips each discharge class with multiple sub‑prototypes to explicitly model diverse intra‑class morphological patterns and provide complementary discriminative cues, alleviating recognition difficulties stemming from intra‑class morphological diversity and inter‑class feature similarity. Experiments on our self‑constructed PRPD dataset covering six discharge classes show that MCP‑MMLoP adds merely 0.0092M additional trainable parameters over the MMLoP baseline and achieves state‑of‑the‑art performance, which validates that our framework enhances discriminative capacity for complex PRPD samples while retaining the parameter‑efficiency benefits of low‑rank prompt learning.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
phase-resolved partial discharge, multi-modal, low rank prompt learning, multi-center prototype learning

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_gAT2OpenReview ↗
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Paper summary

This paper proposes MCP-MMLoP, a parameter-efficient framework for phase-resolved partial discharge (PRPD) recognition. It augments multimodal low-rank prompt learning on a frozen CLIP backbone with a multi-center prototype module that represents each discharge class using multiple sub-prototypes. Entropy-weighted EMA updates and intra-/inter-class regularization are used to stabilize the prototypes and improve class separation. The two branches are fused for final classification. The method is evaluated on a self-constructed dataset of 1,694 PRPD patterns covering six classes. Comparisons with prompt-learning and LoRA-based baselines, together with ablation, few-shot, sensitivity, visualization, and convergence analyses, show that MCP-MMLoP achieves 98.9% overall accuracy and 99.0% macro-F1 with approximately 20.8K trainable parameters.

Critical strengths
  1. PRPD data is typically limited in scale, whereas industrial deployment is often constrained by storage and training resources. The paper freezes the CLIP backbone, training only low-rank prompts and a small number of prototype parameters; the multi-center prototype branch adds only about 9.2K parameters, bringing the total optimizable scale to approximately 20.8K. This design is simple and easily integrated into existing VLMs, while also increasing the metal discharge recall from 92.3% to 97.4% on the current dataset. Such a trade-off between accuracy and parameter size holds practical significance.

  2. The paper not only compares CoOp, CoCoOp, MaPLe, PromptSRC, MMA, CoPrompt, and various LoRA methods, but also provides per-class recall, few-shot results, hyperparameter sensitivity, confusion matrices, t-SNE, and training convergence curves. These analyses clearly illustrate the model's behavior.

Critical weaknesses
  1. The experimental results are primarily derived from a relatively small, private laboratory dataset using a randomly stratified, image-level split. The paper fails to clarify whether samples across different splits originate from the same equipment, defective specimens, acquisition batches, or continuous measurement sequences. Consequently, there is a risk of correlated samples leaking across the training and test distributions, which is insufficient to support claims of "state-of-the-art" performance and robust real-world generalization.

  2. The low-rank multimodal prompts, UDC, and consistency constraints are largely drawn from existing work like MMLoP, which already proposed a low-rank multimodal deep prompting framework with approximately 11.5K parameters. Furthermore, the combination of multi-center prototypes, entropy-weighted EMA, intra-class compactness, and inter-class separation bears a striking resemblance to the MCPE framework cited in the paper, which has already applied these core mechanisms to fault diagnosis scenarios. Therefore, the current core contribution leans closer to combining two existing methods and applying them to PRPD rather than introducing a genuinely novel learning mechanism, resulting in limited methodological novelty.

  3. In addition, the main text and appendices present inconsistent descriptions regarding the prototype updating scheme, and the entropy weights lack sufficient justification. The entropy definition provided is neither the complete class distribution entropy nor the sample-wise prediction entropy. Consequently, the inverse entropy weights can become disproportionately large, yet no stabilization term or clamping mechanism is discussed in the manuscript.

Questions for authors
  1. How many distinct devices, defective specimens, acquisition batches, and independent experiments do the 1,694 samples originate from? Were continuous acquisitions split or rendered into multiple PRPD images? Furthermore, are the training, validation, and test sets completely mutually exclusive at the level of devices, specimens, and acquisition sessions?

  2. Why is a class-margin term used instead of the full batch-level class entropy or sample-wise prediction entropy?

  3. Beyond combining the two branches and applying them to PRPD, what substantive new contributions does this paper offer in terms of learning objectives, prototype updates, or theoretical mechanisms compared to MMLoP and the published MCPE?

  4. Refer to the Weaknesses section for other issues.

Reviewer_nynWOpenReview ↗
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Paper summary

The paper tackles phase-resolved partial discharge (PRPD) pattern recognition, a six-class insulation-defect diagnosis task on power equipment. The proposed MCP-MMLoP framework keeps a frozen CLIP ViT-B/16 backbone and combines two lightweight paths: (i) an MMLoP-style multimodal low-rank prompt path with Uniform Drift Correction (UDC) and a self-regulated consistency loss; and (ii) a multi-center prototype (MCP) path that maintains K sub-prototypes per class, updates them with an entropy-weighted EMA rule, and stabilizes the prototype space with intra-class compactness and inter-class separation regularizers. The two cosine-similarity scores are fused by a fixed coefficient β = 0.5. Experiments are reported on a self-constructed dataset of 1,694 PRPD patterns (1,353 train / 167 validation / 174 test), comparing against zero-shot CLIP, CoOp, CoCoOp, MaPLe, PromptSRC, MMA, CoPrompt, CLIP-LoRA, Block-LoRA, Comp-LoRA, and MMLoP. The authors report 98.9% OA and 99.0% macro-F1 with 20.8K trainable parameters, versus 97.7% OA for the MMLoP baseline.

Critical strengths

Clear practical motivation. Automated PRPD defect diagnosis is a relevant power-system application, and the paper explicitly frames the two domain difficulties it targets: intra-class morphological diversity and inter-class feature overlap. Reasonably broad PEFT baseline coverage on the parameter dimension. Table 1 compares the method against the standard prompt-learning family (CoOp, CoCoOp, MaPLe, PromptSRC, MMA, CoPrompt) and several LoRA variants, and the appendix documents hyperparameters, augmentation, and a training pseudocode (Algorithm 1). Engineering completeness. The paper includes t-SNE visualizations, silhouette scores, an EMA-momentum sensitivity sweep, a confusion matrix, a convergence curve, and a preliminary error analysis in Appendix C. A sensible heuristic in spirit. Using class-level entropy to down-weight uncertain classes when updating prototypes is a reasonable stabilization idea for noisy, morphologically heterogeneous classes.

Critical weaknesses

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.

Questions for authors
  1. Statistics. Please report OA and macro-F1 as mean ± standard deviation over at least five random seeds, with bootstrap 95% confidence intervals on the test split and a paired McNemar's test versus MMLoP and MMA. On a 174-sample test set, justify why the 1.2-point OA gain over MMLoP is significant.
  2. Dataset and benchmarks. Release the PRPD dataset (or a public subset) together with class-level supports; if no public PRPD benchmark exists, validate on at least one external published PD dataset and report cross-device / cross-condition generalization.
  3. Core ablation. Add a K = 1 single-center prototype baseline and the full factorial cells: prototype path only; prototype path + L_intra; prototype path + L_inter; uniform EMA versus entropy-weighted EMA; fixed versus learned β; m sensitivity. State explicitly which component produces the 97.7 → 98.9 gain.
  4. Method closure. Provide a dimension derivation for Eq. (1), a clear statement of which prototype tensors are trainable versus stop-gradient, a normalized/batch-averaged EMA rule, and a corrected entropy definition in Eq. (9). Clarify how L_inter gradients reach (or do not reach) the prototypes.
  5. Efficiency measurements. Report inference latency, FLOPs, peak memory, and throughput for every method in Table 1, not only parameter counts.
  6. Few-shot protocol. Provide a full few-shot table with prompt-learning and PEFT baselines at 4/8/16/32 shots, along with episode statistics and mean ± variance.
  7. Baseline fairness. Explain why the CNN/LSTM/MobileNet/capsule/metric-learning PRPD methods reviewed in §2.1 were excluded from Table 1, and add at least the strongest such baseline for comparison.
  8. Shortcut analysis. Analyze the near-perfect Normal-class accuracy: report accuracy after noise-level matching, and inspect whether decisions rely on amplitude/background statistics rather than discharge morphology.
Reviewer_LPy4OpenReview ↗
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Paper summary

The paper extends multimodal low-rank prompting for a frozen CLIP backbone with multiple prototypes per discharge class. Classification adds a weighted nearest-prototype similarity (β = 0.5) to the text-image similarity. An entropy-weighted exponential moving average updates prototypes, while compactness and separation losses aim to improve feature geometry. Experiments use a six-class laboratory PRPD dataset containing 1694 images.

Critical strengths
  1. The proposed prototype branch addresses a plausible application problem: a discharge class can contain several distinct visual patterns. The additional parameter cost is small (about 9.2K parameters), and the approach integrates naturally with the existing prompting framework.
  2. The reported results improve upon a reasonably broad collection of adaptation baselines. Table 1 reports 98.9% accuracy and 99.0% macro-F1, compared with 97.7% and 98.1% for MMLoP. The alternate manuscript in the supplementary archive labels its results as means over five seeds and specifies a paired t-test. However, the main PDF states no repetition protocol, and the released scripts do not substantiate the claimed five-seed baseline comparisons or repeated random partitioning (see Weakness 2). This evidence therefore needs clarification before it can carry weight.
Critical weaknesses
  1. The prototype optimization procedure is internally inconsistent, and the released code matches neither written description. Section 3.5 and Algorithm 1 describe EMA updates. Appendix A.2 instead states that prototype parameters are updated by back-propagation, with a separate 1e-4 learning rate. The inter-class loss in Equation 12 is a function of the prototypes alone, so it never provides a direct gradient to the low-rank prompt parameters. Under the EMA-only procedure of Section 3.5 and Algorithm 1, it would update no parameter at all. The released code takes a hybrid approach. Prototypes are an nn.Parameter optimized by AdamW at the same 1e-3 learning rate as the prompts, not the stated 1e-4, and a no-grad EMA step is applied on top (trainers/mmlop.py:478, 729-730, 770-815). The inter-class loss therefore moves only the prototypes and reaches the prompts only indirectly, through later cross-entropy and compactness terms. The manuscript should describe and justify this hybrid procedure, ideally with ablations comparing gradient-only, EMA-only, and hybrid updates.

  2. The evidence does not sufficiently isolate the proposed mechanism or establish generalization.

    • Uncertainty weighting. Section 3.5 defines q_n as a soft label without specifying how it is obtained. In the released code, q_n is the prototype-path softmax prediction at τ = 0.07 (mmlop.py:795). The code also departs from Equations 9-10. It uses w_c = 1 - H_c/log C, and it applies the ground-truth class's weight to a per-cluster mean feature, so the per-sample weight w̄_n is never formed (mmlop.py:799-815). Because H_c = -p̄_c log p̄_c is at most 1/e, w_c stays within about [0.79, 1] for six classes. The entropy weighting therefore changes the EMA step by at most about 20%. Because q_n enters only through batch-averaged class marginals, the statistic cannot distinguish confident from diffuse predictions that share the same class averages. A matched ordinary-EMA control is consequently important.
    • Split design. Evaluation uses a small, randomly split (8:1:1, stratified) laboratory dataset. The manuscript does not establish whether physical specimens or acquisition sessions are disjoint across partitions.
    • Repetition and significance. The supplementary manuscript states that results are means over five seeds, used "to reduce the effect of random partitioning", and that a paired t-test (α = 0.05) was applied against the strongest baseline. The released materials do not substantiate this. The loader reads pre-existing train/val/test folders, so the seed does not re-partition the data within the released pipeline (datasets/custom6.py:173-181, 247-249). The supplied baseline scripts specify seed 1, and only run_mcp_mmlop.sh defaults to five seeds. These files cannot show whether the authors used other commands or externally regenerated splits, and the absence of t-test code is a reproducibility limitation rather than evidence that no test was performed. The paper reports only "p < 0.05", without an exact p-value, per-seed results, or dispersion, and the unit of pairing is unclear. The authors should clarify the actual experiment commands, split-generation procedure, and paired results.
Questions for authors
  1. Are prototypes updated by gradients, EMA, or both? The code trains prototypes by AdamW at 1e-3 and also applies EMA. Please reconcile this with Algorithm 1 (EMA only) and with Appendix A.2/Table 5 (back-propagation at 1e-4), and explain the gradient path through which the inter-class loss changes the model.
  2. How does the full method compare with an otherwise identical multi-center model using ordinary EMA? Please report paired seed-level results and uncertainty estimates, the exact p-value, and what was paired in the stated t-test. Were the baselines in Table 1, and the ablation and momentum studies in Tables 2-3, also run with five seeds? The supplied baseline scripts specify seed 1 and use pre-existing partitions. Please provide the commands, seeds, and split-generation procedure used for the baseline comparisons and the ablation and momentum studies. The released momentum_experiment.py also differs from the reported setup. It uses seed 1, one center (K = 1 vs. 3), β = 1.0 (vs. 0.5), batch size 4, and 70 epochs. It also passes η directly to EMA_MOMENTUM, which the code interprets as 1 − η (train.py:150). Please confirm the configuration that produced Table 3.
  3. Are acquisition sessions and physical specimens disjoint across partitions? If repeated measurements exist, can the method retain its advantage under a grouped split?

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