- Rating
- 4(+2)
- Confidence
- 3
- Informativeness
- 3
- Presentation
- 3(+1)
- Soundness
- 3(+1)
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Paper summary
This paper introduces wARV, a weight-space metric measuring neural network similarity without using data probes. wARV is based on the Ahmad RV coefficient, computed on the chain weight matrix of the neural network. Some layer types require adaptations or approximations.
The authors perform multiple experiments to demonstrate the capabilities of wARV. They show that their metric is very capable when trying to identify the task a model is trained on, including cross-architectures. They further note that their metric evolves throughout the training of the model, and can also capture differences such as adversarial training. They finally demonstrate that wARV evolves gradually with incremental mixes of training tasks.
Critical strengths
I find this paper very interesting, and like the idea behind wARV. This paper has, in my opinion, strong potential.
- S1 - Significance: wARV overcomes several limitations of existing methods to compare neural networks. First and foremost, it is not limited by the need to choose and use probes. Then, compared with other weight-space metrics, it is invariant to the intertwiner group, e.g. permutations. It therefore has the potential to become a standard distance metric for weight space learning.
- S2 - Results: Experimental results look promising. There is a relatively strong correlation and predictive power between wARV and training task. Cross-architectural compatibility of wARV is another strong advantage of the metric.
Critical weaknesses
In its current state, I still think, however, that this paper has key weaknesses. I look forward to the discussion period to see the authors’ opinion on these.
- W1 - Experiment setup: I find the experiment setup quality uneven throughout the paper. While Sections 4.1 and 4.4 are mostly clear, I have more difficulty with Sections 4.2 and 4.3. In 4.2, the authors use the AUROC metric, including for individual models, but do not detail how the predictions are performed, or what splits are used. It is also unclear what probes are being used for the cosine similarity between logits. In 4.3, the authors show a difference between normal and adversarial training using visual inspection of distribution curves: why not re-use the same metrics as in Section 4.2 to see whether wARV effectively classifies those two training schemes?
- W2 - Limitations: I think that the authors insufficiently explore and discuss the limitations of wARV. It is, however, crucial to do so: if one wants to use a metric, one should know to what it applies, and to what it does not. First, wARV omits nonlinear activations (except after batch normalisation layers) and bias terms: is that critical in some cases? What happens when activations are not in the extended ReLU family? What happens when the neural networks use biases? Furthermore, wARV uses several approximations, for example to represent attention or residual connections, and we see in the experiments that performance in larger BMLP and ViT drops, probably because of this. This raises questions: what would the performance of wARV be on even larger networks? For example, ViT-Small is twice as large as the larger ViT seen in the paper. Under what conditions would wARV fail because of these approximations? Finally, we see that wARV shows strong performance mostly for identifying the training tasks, and authors note that it works less well to identify training hyperparameters such as initialisation or batch ordering: it would be helpful for the conclusion to address what wARV can help measure, and what it cannot.
Questions for authors
Please refer to the Weaknesses Section.
6 comments
Response to the authors' rebuttal
Dear authors,
I have read through your rebuttal and the other reviews, and I appreciate your on-point responses.
W1: Experiment setup is now much clearer to me. On Section 4.3, the quantitative result is appreciated. As discussed in your rebuttal, I find it perfectly acceptable that wARV carries less discriminative power regarding adversarial training. As long as the elements in the rebuttal are all written into the revision, I consider this weakness addressed, thank you.
W2: I remain convinced that a proposed metric such as wARV should be tested and proven on a wide variety of cases to be useful as a metric, and therefore for acceptance at a conference such as ICLR. Testing wARV on common designs like bias terms or realistic-size ViT is, in my opinion, needed. I unfortunately cannot see W2 as completely addressed without these additional experiments, since the limited scope in which wARV is tested would in turn limit the significance of the metric. I mostly agree with the rest of your remarks in your response.
Related to the other reviews. Both other reviewers highlighted existing works in the same area as wARV, which I also did not know about. Do you think it would be relevant to compare wARV to at least Chen et al. (2023) - which I am not familiar with, in a similar way as the authors compare wARV with cosine similarity on logits? It would be helpful in understanding the differences between both metrics.
In general, I would reiterate that I see strong potential in this paper. However, with the proposed method being a metric, I think the scope in which it is tested and proven remains at this stage too narrow and therefore negatively affects the significance of wARV.
Reviewer zGjA
Larger ViT experiments, bias clarification, and similarity benchmark
We thank the reviewer for encouraging us to test wARV in additional settings. Below, we provide additional evidence and clarify the remaining limitations. We would appreciate feedback on whether these additions address the reviewer's concerns.
1. wARV on a realistic-size ViT
We computed wARV across publicly available OpenCLIP ViT-B/32 training checkpoints, similar to the analysis of BMLP training dynamics in Fig. 3a. This model has ~150M parameters. Here we report wARV between checkpoints at different epochs:
| epoch b \ a | 1 | 2 | 4 | 8 | 12 | 16 | 24 | 28 |
|---|---|---|---|---|---|---|---|---|
| 2 | 0.22 | |||||||
| 4 | 0.11 | 0.55 | ||||||
| 8 | 0.07 | 0.40 | 0.60 | |||||
| 12 | 0.07 | 0.40 | 0.58 | 0.72 | ||||
| 16 | 0.10 | 0.36 | 0.54 | 0.67 | 0.72 | |||
| 24 | 0.05 | 0.17 | 0.29 | 0.33 | 0.38 | 0.39 | ||
| 28 | 0.05 | 0.11 | 0.19 | 0.24 | 0.28 | 0.25 | 0.91 | |
| 32 | 0.05 | 0.11 | 0.17 | 0.21 | 0.25 | 0.23 | 0.89 | 0.99 |
From epochs 1 to 16, wARV recapitulates expected training dynamics: nearby checkpoints generally have higher similarity than more distant checkpoints, and similarity between nearby checkpoints increases as training converges. Notably, epochs 24–32 form a highly similar group, with only moderate similarity to earlier checkpoints. This suggests a change followed by stabilization in the weight structure captured by wARV, may indicate a transition between local basins with prolonged training. We will include this result (as a heatmap similar to Fig. 3a) in revision.
2. wARV on models with bias terms
We apologize that this was unclear: every model evaluated in our experiments, including MLP, BMLP, LeNet, ResNet, and ViT, contains bias terms. Thus, our experiments already evaluated wARV on models with biases, although the chain weight approximation omits these terms. Our exploratory attempts to combine chain weight and bias information did not consistently improve the results and sometimes degraded them, we thus focused on weights alone. Our findings suggest that weights alone capture significant aspects of model variation, and that bias and nonlinearity may not play as an important role in learnt variation as weights.
3. Comparison with other similarity measures, particularly Chen et al.
We agree that comparing wARV with measures beyond logit cosine similarity is important. In our exploratory work, we compared wARV with functional similarities based on accuracy, prediction, Jensen–Shannon divergence of probabilities, besides logit cosine similarity, as well as with representational similarities Procrustes and Centered Kernel Alignment (CKA). Notably, Chen et al. (2023) report a correlation of 0.955 between CKA and their method in Fig. 2.
We will include the following benchmarking result in revised SI:
We considered 50 pairs of independently initialized, untrained networks and 50 pairs of consecutive checkpoints near the end of training, serving as low- and high-similarity reference anchors, respectively. We report here similarity values (mean ± SD). The separation gap Δ = min(consecutive-checkpoints similarity) − max(random-network similarity); larger positive values indicate better separation between anchors.
| Measure | Random networks | Consecutive checkpoints | Separation gap Δ |
|---|---|---|---|
| Accuracy similarity | 0.98 ± 0.02 | 1.00 ± 0.00 | −0.01 |
| Prediction agreement | 0.10 ± 0.09 | 0.99 ± 0.01 | +0.63 |
| Logit cosine | 0.09 ± 0.12 | 0.98 ± 0.02 | +0.55 |
| 1 − JSD(probability) | 0.98 ± 0.00 | 0.99 ± 0.01 | 0.00 |
| Procrustes | 0.88 ± 0.02 | 0.99 ± 0.01 | +0.03 |
| CKA (0.955 correlation with Chen et al.) | 0.71 ± 0.10 | 0.98 ± 0.02 | +0.06 |
| wARV | 0.00 ± 0.00 | 0.98 ± 0.02 | +0.93 |
Among the measures evaluated, wARV is the best calibrated: it has a tightly concentrated baseline near zero for independently initialized networks, versus similarity near one for consecutive late-training checkpoints.
We prioritize these widely used measures because they apply to independently trained models across architectures. Functional similarity has been used as near groundtruth in previous studies evaluating representational similarity, our reply to Reviewer k1Zy explains our choice of logit cosine as a representative functional measure. While we are impressed by Chen et al.'s method, it assumes filter-atom decomposition with layerwise shared atom coefficients, and we did not find publicly available checkpoints in such setting.
Response to Reviewer: Experiment setup and Limitation
We thank the reviewer for identifying unclear experimental details and for encouraging a more explicit discussion of the limitations of wARV. We will revise Sections 4.2 and 4.3 to increase clarity and add a separate Limitations section. We would appreciate feedback from the reviewer on whether these proposed changes fully address their concerns.
W1. Experimental setup and logic
Whereas Section 4.1 reveals that some comparisons discriminate models by training task, it does not guarantee meaningful cross-architectural comparisons. Section 4.2 examines this through binary classification: AUROC quantifies how well wARV detects whether cross-architectural model pairs were trained on similar tasks, treating MNIST and EMNIST digits as the same task.
We use a simple prediction rule: "two models were trained on the same task if their wARV value exceeds a threshold." We took 1000 evenly spaced thresholds and computed the true/false positive rates for each. Since the goal is to quantify discrimination, no classifier is fitted and no separate train/test split is used. Fig. 2b reports AUROCs for comparisons involving the indicated architecture and other architectures, not individual models' predictive accuracies.
For cosine similarity of logits, we use 1000 training images, with 200 selected from each of the five task datasets.
Section 4.3 examines additional sources of variation in controlled settings. For discriminating model pairs trained using the same versus different methods (standard/adversarial), AUROC is 0.597 (95% CI [0.582, 0.610]), consistent with a smaller contribution of training method to variation in wARV.
W2. Limitations and interpretation
Omitting nonlinear activations results in loss of information when constructing the chain weight matrix. We suggest approximating activations where practical (Appendix B.6), particularly in pre-normalized skip connection blocks (B.7). Our invariance proof covers ReLU, leaky ReLU, and GELU. For other activations, invariance depends on the corresponding intertwiner group and is not guaranteed in general.
Regarding bias terms, the methods detailed in Appendix B can be extended to compute an analogous "chain bias vector," retaining invariance under the same symmetries. We explored combining cosine similarity of chain biases with wARV using a weighted sum, but we elected to focus on the weight component only for this paper. Models differing only in omitted bias terms can have identical wARV despite having different functions.
We agree that the chain weight matrix may lose critical information, especially for larger and deeper models. For example, our attention approximation omits the query and key matrices and cannot detect differences confined to those parameters. We have not established reliability for ViT-Small or a model-size threshold for approximation failure. Stress testing, customizing, and scaling wARV to larger models are important future directions.
However, a lower AUROC does not necessarily imply less accurate measurement. It can imply weaker discrimination of the specified factor, which may reflect other sources of learned variation as well as approximation error. AUROC should not be treated as the sole measure of wARV's validity.
We expect lower discrimination for subtler factors such as adversarial training. Trained models differing only in initialization or batch ordering are considered highly similar by wARV. This is consistent with the conjecture that SGD solutions can lie in a common basin after accounting for hidden-neuron permutations (Entezari et al., 2022), although wARV alone does not establish mode connectivity. When these random factors do not meaningfully alter what models learn, chance-level discrimination is desirable.
Our goal is to detect whether models learn similar "knowledge," rather than maximize discrimination of every training factor. The weights are updated through training while activation functions remain fixed. Our results show that these weights alone preserve substantial information about what models have learned: wARV identifies task as the dominant source of variation, detects subtler changes associated with training method, and recapitulates expected training dynamics.
We view wARV as a general framework, not a fixed method, and welcome extensions incorporating bias terms and alternate nonlinearities. As discussed in the paper, potential applications include studying linear mode connectivity and constraining unintended model changes during machine unlearning or interpretability interventions. High wARV, however, does not guarantee preservation of all functional behavior.