Paper: A Symmetry-Aware Exploration of Bayesian Neural Network Posteriors (ICLR-2024)

Reviewer comment (Theory):
[W1] **Lack of clarity**. There are some statements whose scope/explanation is not quite clear to me: “The scaling operation (...) is a symmetry for all neural networks” (Property 3.2); “neural networks seem to always be subject to scaling symmetries” – I feel this should be restricted to ReLU-type nonlinearities. Why does this hold in general?

Author response:
- **Concerning the lack of clarity [W1]**, we thank the reviewer for pointing out that our phrasing in Property 3.2 is imprecise. Since we cannot develop the full formalism in the core paper, we decided to restrict it to two-layer perceptrons. However, symmetries are not restricted to this case, and the sentence highlighted by the reviewer aimed to convey that our work tackles other architectures. In this paper, we focus on ReLU-activated neural networks and confirm that properties on the scaling symmetries only hold in this case. We have rephrased this sentence in the updated document for clarity.

Reviewer comment (Theory):
[W1] **Lack of clarity**. There are some statements whose scope/explanation is not quite clear to me: More generally about the *min-mass* problem: What, exactly, is the implication? Do we impose a second, ex-post minimization problem over the solution of standard training? How comes the problem is convex if existing literature on [representation costs](https://openreview.net/pdf?id=6iDHce-0B-a) (which tackles the same problem and is not cited?) turns out not to be a convex problem?

Author response:
- **Continuing on [W1]**, the main implication of the min-mass problem is, to our understanding, that we cannot rule out the impact on scaling symmetries when focusing on the posterior. Supposing that neural networks empirically converge to the minimum of this problem, it would mean that scaling symmetries do not play any role on the posterior. The difficulty with scaling symmetries is that, contrary to permutation symmetries, we cannot make their role explicit, as they actively interact with the main training loss. We do not think that we need to run another optimization since this would only result in a lower regularization term, which is without impact on the actual performance of the models. However, it is unclear for now, but minimizing this term could have an impact on fine-tuning, for instance.

We thank the reviewer for the exciting reference on representation costs that we missed. We are currently reading it in detail; however, our hypothesis is that - in our paper - we reduce the size of the domain of the variables (to strictly positive vectors for the lambdas) and exhibit the explicit impact of scaling symmetries on the weights. It seems that Arthur Jacot’s work is somewhat more general, tackling all possible weight symmetries, whereas we restrict ourselves to scaling symmetries (you may see the work of Rolnick et al. [**2**] on the other “hidden” symmetries for further details). For completeness, our sketch of proof of the log-log strict convexity of the min-mass problem is available in Appendix C.7.3.

Reviewer comment (Writing):
[W1] **Lack of clarity**. There are some statements whose scope/explanation is not quite clear to me: “All the layer-wise marginal distributions are identical” (Proposition 1) – how so?

Author response:
- **Continuing on [W1]**, given that the posterior is a mixture of all permutations, marginalizing any neuron in a given layer will lead to the same distribution. We can detail this point if it is not clear or convincing enough.

Reviewer comment (Theory):
[W2] **Conflating Bayesian and risk-minimization perspectives**. The paper is supposed to be about BNN posteriors, yet most claims and analyses focus on standard network training. It would be useful to elaborate more on both perspectives, or reconcile them. E.g., what do Definition 3.3 / Proposition 2 mean for a Gaussian prior equivalent to L2 regularization? As-is, the impact of the paper for actual Bayesian inference remains unclear.

Author response:
- **Regarding the Bayesian perspective [W2]**, we chose to focus our paper on the posterior, a part of the Bayesian framework that has been recently exposed as one of its most important aspects (e.g., in [**1**]) and that remains not fully understood. Concerning Definition 3.3, the fact that modern neural networks undergo scaling symmetries that modify the L2 regularization term without functional changes can lead us to slightly update our interpretation of the regularization term as Ockham’s razor. Notably, this again stresses that the mass of the network is a very simplistic heuristic of the complexity of the resulting model.

Reviewer comment (Experiments):
[W3] **Unclear baseline / omissions in experiments**. Somewhat related to [W2]: I don’t quite understand how the “true” posterior distribution, w.r.t. which the MMD is reported, is computed. How, exactly, is the RKHS constructed? Also, I feel that the Bayesian perspective is quite under-represented with only one MCMC method (the other methods present have no guarantees of retrieving the true posterior).

Author response:
- **Concerning the unclear baseline/MMD [W3]**, we are rewriting the paragraph on the Maximum Mean Discrepancy to clarify this part of the paper. We will come back to you when this is done. In the meantime, we recall that we independently train 1000 DNNs that we use as target samples for the MMDs that we compute on 20 different kernels, as in Schrab and Gretton et al. [**4**]. We provide different statistics on these kernels in Table 2.

- **Continuing on [W3], for the baseline omissions**, we agree that we present only one strictly MCMC method and that it is not fully satisfactory. However, we tackle real-world datasets/architectures in this work, and many MCMC methods cannot scale to these problems. We propose to add stochastic Langevin dynamics [**5**] in the next update of our paper on MNIST. We will come back to you when integrated into our work.

Reviewer comment (Writing):
[Q2] What kind of objects are $\Pi$ and $\mathbb{\Pi}$?

Author response:
- **[Q2]** Let us take a neural network with $k+1$ layers, $\Pi$ is a set (ordered) of $k$ permutation matrices. The size of each permutation matrix is adapted to the corresponding hidden dimension of the network at this layer. In our paper, we chose to formalize permutations with matrices for clarity. Of course, they are implemented by operations on indices in our codes for computation efficiency. $\mathbb{\Pi}$ is the set of possible sets of permutation matrices for a given architecture. To further improve the clarity, we added a Table including the main notations of the paper at its end.

Reviewer comment (Evaluation):
[Q5] Why are single-mode methods competitive in terms of ECE? Is there a tendency towards either over- or underconfidence?

Author response:
- **[Q5]** This remark is shared with reviewer **Mjnv**. Considering the criticisms on the equal-width binned ECE, we have added the adaptive calibration errors (ACE) to Table 1. We show that OptuNets - very shallow networks - exhibit underconfident behavior and provide the calibration plots in the case of the BNN and Multi-BNN in Appendix B.4. We can provide more plots corresponding to other methods and architectures if desired.

Reviewer comment (Theory):
[Q7] What is your idea behind connecting functional collapse to OOD performance?

Author response:
- **[Q7]** The mutual information - which emerges when the predictions of elements in the ensemble differ - is often used to quantify epistemic uncertainty, although its relevance has also been disputed [**3**]. In this last section, we uncovered that, at least in our setting, couples of independently trained neural networks tend to exhibit similar quantities of diversity on in-distribution and out-of-distribution data. If this were not the case, ensembles could collapse in the function space despite their weight-space differences. In this case, we would not gain much from ensembling. These experiments tend to show that this is not a risk in practice.

Reviewer comment (Writing):
The paper as a whole presents a meandering set of concepts and results, without drawing conclusions or presenting insights into further study of Bayesian method design. This is apparent from the conclusion section, which is vague and raises questions: what are the actual insights provided by considering symmetries? What questions and hypotheses would you consider in future work? What was the “real impact of scaling symmetries”?

Author response:
**Concerning the lack of conclusive Insights [W1]:** We acknowledge your feedback on the clarity and would like to provide additional clarification. Our paper aims to explore all the different aspects of the interaction between weight-space symmetries and the posterior, all of which remained vastly unchartered. Our work introduces several novel contributions: firstly, we are among the pioneers in sharing the ground truth of DNN posteriors; secondly, we contribute to the field by establishing equation 8 (without debatable hypotheses), which provides a first explanation of the links between posterior and weight-space symmetries and explains the patterns that practitioners encounter when visualizing posterior estimations. Thirdly, we explore the connection between the quality of posterior estimation and the effectiveness of uncertainty quantification by comparing distributions of extremely high dimensions. Finally, we provide in Section 5.1 a result that is important for the practitioners and which updates (upwards) the confidence that we can grant to the ubiquitous _deep ensembles_.
In contrast to a large part of the papers in the surrounding field, our analysis tackles real-world architectures. We would like the reviewer to keep in mind that implementing experiments on the posterior distributions of these models is an extremely complex task. For example, it is impossible to obtain direct estimations of the value of this posterior in a bin of weight space, given that we cannot choose where the model will converge. This is an important limiting factor for our experiments, which may be important to consider.

Reviewer comment (Evaluation):
The experiments presented do not provide evidence for the claim presented in the method section: "SYMMETRIES INCREASE THE COMPLEXITY OF BAYESIAN POSTERIORS" (see questions below). Nor do they study interventions informed by the theory to evaluate the benefit of the formal treatment of scale and permutation symmetries.

Author response:
**Concerning the limited empirical demonstration that the symmetries increase the complexity of Bayesian posteriors [W3],** we understand your concern that the MMD does not definitively prove that removing symmetries improves posterior estimation given the challenges of high-dimensional distributions. Again, experiments on the posterior of modern networks are particularly complex and were previously mostly unchartered. However, we will incorporate more straightforward distances into our work to improve the clarity of this side of the paper.

Reviewer comment (Experiments):
The reported accuracies in Table 1 are low. While this is understandable for the purposefully restricted OptuNet, a vanilla single-mode baseline resnet-18 model on cifar-100 can reach 75% accuracy without any Bayesian treatment, and with some tuning 79%. (https://paperswithcode.com/sota/image-classification-on-cifar-100 https://huggingface.co/edadaltocg/resnet18_cifar100). It seems the results and the presented checkpoint dataset represent an artificially underfitted model space. If the aim is to improve Bayesian deep learning for a real-world setting, it might be beneficial if the models studied are optimized to a reasonable performance.

Author response:
**Regarding the performance of our ResNets [W4],** our initial accuracy was lower due to our focus on obtaining a pure posterior unaffected by data augmentations. After a code review, we noticed an issue with the batch normalization. We have updated the results and are achieving close to 80% accuracy with deep ensembles. Unfortunately, it is unclear whether achieving very high single-model performance (79%) without data augmentations is possible. We hope that this corrected performance will be satisfactory.

Reviewer comment (Writing):
What do you mean by ‘regroup some points around the modes’ in section 3.1? What causes this effect and how is it problematic?

Author response:
**Concerning the sentence on the high-level impact of scaling symmetries [Q1],** we thank the reviewer for highlighting that it is unclear. We meant that removing the scaling symmetries tends to regroup the points around the main modes. Equation (8) sheds light on this matter, showing that functionally equivalent networks can be dispersed due to these symmetries. Formally, removing the symmetries means removing the dispersion due to the continuous mixture over the possible scales. We do not argue that this is a problem, but rather information that the practitioners could be interested in to achieve a more in-depth comprehension of deep learning models.

Reviewer comment (Reproducibility):
How is the “target distribution with 1000 checkpoints” for table 1’s MMD scores established? What method is used to determine this distribution?

Author response:
**Regarding the target distribution for the MMD [Q2],** we will include a detailed explanation of our MMD calculation in the next version of the document. To provide a clearer understanding, the MMD involves mapping the checkpoints into a Hilbert Space, computing the empirical mean, and subsequently determining the distance between these empirical means. Notably, the empirical MMD exhibits convergence in probability at a rate of O((m + n)^(-1/2)) to its true value, where $m$ and $n$ denote the number of samples in each set. This convergence demonstrates the reliability and consistency of the MMD.
As explained in Section 4.1, on which we are currently working, we use 1000 independently trained checkpoints as the target sample. Please note that the results of all methods are based on networks that were not used in the target samples to avoid biasing the MMDs.

Reviewer comment (Evaluation):
I am not sure what to take away from Table 1 and section 4.1-4.3. The study of uncertainty quantification performance of these methods has been done before, how does this experiment connect to the formal study of scale and permutation symmetries?

Author response:
**On the connection of symmetries and uncertainty studies [Q3]:** The link to prior uncertainty studies lies in the fact that all the uncertainty estimation techniques we assess require some form of posterior estimation. However, most researchers typically validate this estimation solely on the quality of the uncertainty estimation (mostly proper scores like the NLL and Brier score, calibration like ECE and ACE, and out-of-distribution detection). We believe it is legitimate to evaluate the quality of the posterior estimation and explore whether there is a correlation with the quality of uncertainty quantification. Moreover, Table 1 highlights the non-trivial benefits of multi-mode methods compared to single-mode, notably in estimating epistemic uncertainty and its downstream impact on the detection of out-of-distribution samples. Furthermore, the table presents quantitative evaluations of the different mainstream uncertainty quantification methods on a larger scale than usual (especially for SGHMC) - the experiments being scaled up to TinyImageNet - and with many more metrics than usual. Indeed, usual benchmarks are often restricted to Accuracy, ECE, and NLL. Additionally to our new posterior quality metrics, we report another proper score (Brier), performance in OoD detection using the Mutual Information, as well as quantitative metrics of the diversities of the predictions, both in and out of distribution. The update of the document now adds one more reliable metric for top-label calibration (ACE) that readers can consider in their evaluation of the different methods at play.

Reviewer comment (Experiments):
Similarly, how does the study of ‘functional collapse’ in Figure 3 and section 5.1 suggest that  “complexity of the posterior is orders of magnitude higher than what we understand, taking symmetries into account.” I don’t follow how symmetries were taken into account in this study, and what to take away from this to improve the Bayesian treatment of neural networks. It appears to me that the symmetries in the neural networks studied here were left untreated, and no interventions were made to reduce the complexity of the Bayesian posterior through these symmetries.

Author response:
**Regarding symmetries and their link to 'Functional Collapse' [Q4]:** given the extremely high number of permutation symmetries in a modern neural network, $10^{6000}$ for a simple ResNet-18, as well as the infinite number of scaling symmetries (the parameters are continuous), one could expect to find functionally similar neural networks in a large pool of independently trained DNNs. Our experiments in Section 5.1 show that this is not the case. The mutual information measures the functional diversity between two estimators on a given dataset, and we show that, among 500 thousand couples (1000 choose 2) of independently trained ResNet-18, none exhibit low functional diversity (functional collapse). That is, all couples have quantitatively more or less the same diversity. This hints that regardless of the huge size of the space of (nearly-)equivalent functionals, the complexity of the posterior is such that we empirically never fall into this space.

Reviewer comment (Evaluation):
For section 5.2, what is the insight gained from the study of weight permutation? Is “a variation in the Πs” somehow problematic? How does this inform the design of Bayesian deep learning methods?

Author response:
**Insights from weight permutations [Q5]:** Weight permutations are an important aspect for understanding Bayesian neural network strategies. Some of them, like weight averaging, as mentioned in [**2**], could be impacted if weights undergo permutations. This is why some papers, such as [**1**], suggest removing symmetries to facilitate weight averaging. BNNs employing weight averaging, like those found in [**2**, **3**], and [**4**], appear to benefit from stabilizing and averaging weights when the neural network ceases to exhibit permutations.

Reviewer comment (Novelty):
I think the first part of the paper regarding the symmetries is a bit extensive and insights from it are somewhat limited. To the best of my knowledge, it has been known for a while that the BNN posterior effectively consists of a mixture over such symmetries, so I don’t see much novelty in equation (8). While it sets up the subsequent discussion very nicely, I wouldn’t advertise this as one of the core contributions of this work. The in-depth study of the role of the scaling symmetry on the other hand is novel to my knowledge and fosters a better understanding.

Author response:
**On the lack of novelty on the theoretical part [W1],** we want to emphasize that while many papers in the literature focus on symmetries and loss landscapes [**6**, **7**, **8**], the key focus of our paper is on uncertainty. Although symmetries are briefly mentioned in some works [**5**], the posterior's intricacies are often overlooked due to its experimental complexity compared to the loss. However, we argue that quantifying uncertainty, particularly through the posterior, is crucial. 
More specifically, if you feel that we miss an important reference - that justifies the lack of novelty - on the theoretical side of our paper, especially the posterior as a mixture, we would be extremely interested and grateful.

Reviewer comment (Experiments):
An important aspect of the experimental setup, which is however almost not discussed at all, is the choice of “gold standard” for the posterior, to which all other approximations are compared against. This choice is of course crucial for the empirical evaluation! If I understand correctly, the authors chose a deep ensemble consisting of 1000 members. I’m a bit unsure regarding this choice, as it is quite controversial to what degree deep ensembles really implement an approximation to the Bayesian predictive distribution. There are several works arguing for yes [1, 2], while others oppose this view (to some degree) [3, 4]. [4] even argues that repulsive terms are needed to ensure that deep ensembles perform proper Bayesian inference asymptotically. I don’t think that this questions the validity of the experimental setup too strongly, but a proper discussion of this choice and differing view points **have to be discussed** such that readers can make up their own mind regarding this discussion.

Author response:
**Concerning the ground truth posterior [W2],** we appreciate your observation and fully agree. We conducted experiments (as detailed in Section 5.1) illustrating that Deep Ensembles already exhibit some inherent repulsiveness. Yet, we will expand on this discussion in the paper, addressing its importance and the controversial nature of using an ensemble of DNNs as a ground truth posterior. In this new discussion, we notably intend to recall Wild et al. exciting and recent work [**3**].

Reviewer comment (Experiments):
While [2] is cited, the work really lacks a comparison to it. [2] also performs an empirical exploration of Bayesian posteriors and how other approximate methods perform, where the gold standard is full batch HMC. They only evaluate on one dataset (CIFAR10) but I still think this should be compared carefully, and how this work distinguishes itself from [2] should be properly stated. [2] also published their HMC checkpoints, I would really be interested in seeing whether the produced deep ensemble in this work produces a similar posterior. This could also clarify the discussion raised in point 2.

Author response:
**Regarding the comparison to HMC [W3],** we acknowledge the relevance of the suggestion. We have found the checkpoints released by the authors and have started training the ResNet models corresponding to the HMC proposed by [**2**]. It will take some time to ensure that our training procedures are as close as possible to [**2**], which is not trivial as we implement our models in PyTorch and not in JAX. However, we intend to finish this work before the end of the rebuttal period.

Reviewer comment (Reproducibility):
The work is not very careful at introducing a lot of concepts formally. As maximum-mean-discrepancy comparisons are one of the core contributions of this work, I think it would be worth it to formally introduce it in the main text. You also report a metric called NS, which is only described in the caption of Table 1, and I could not find a description in the main text nor a pointer to the Appendix, detailing how the “removal of symmetries” is actually performed. I find this quite an interesting point and I would like to see more discussion regarding how this removal enables a better comparison between different posteriors. Glancing at the numbers, there seems to be no consistent pattern (i.e. MMD sometimes goes up, and sometimes down after removing the symmetries) which is surprising as I would have expected to always see a decrease. Could you elaborate more on this? The multi-modal extension of some of these algorithms is also not clear. Are you simply averaging over all the samples coming from the different modes?

Author response:
**Concerning the formal introduction of the MMD and its results [W4],** removing symmetries improves the histogram estimation but does not necessarily enhance the MMD. We plan to calculate simpler distances between histograms considering that the MMD we used (following Schrab and Gretton et al. [**4**]) is based on multiple kernels, is very complex,  and could bring the data into a Hilbert Space where symmetries are mitigated, potentially improving results. However, we expected MMDs to enable better distance estimation for multi-mode distributions.

Reviewer comment (Evaluation):
The uncertainty estimation results are surprising as the single-mode posteriors consistently perform better. The employed measure ECE has seen a lot of criticism recently [5] so I’m wondering whether a similar problem is at the origin here. Comparing multi-modal and single-modal is maybe also a bit unfair, as the testing accuracies vastly differ.

Author response:
**Concerning the single-mode ECE [W5]:** We agree that the ECE results seem anomalous. As mentioned in response to [**Q1**] (next point), our OptuNets - being shallow - tend to exhibit underconfidence. As suggested, we add the Adaptive Calibration Error (ACE) in Table 1. It confirms that the top-label calibration worsens when taking an ensemble of OptuNet, albeit to a lesser extent than the ECE. To prove the underconfidence of the networks, we provide calibration plots of the BNN and multi-BNN in Appendix B.4. We can provide more plots corresponding to other methods and architectures if desired. We also report in Appendix B.4 the relevant comment that comparing calibration performance is mostly pertinent at similar accuracies. We will acknowledge the quality of the feedback for the camera-ready.

Reviewer comment (Experiments):
Why is your MNIST performance so low? As far as I know even a simple MLP with 2 hidden layers can easily reach $\approx 97\%$ performance.

Author response:
**Concerning the MNIST Performance and Experiment Protocol [Q1],** we agree that we could expect 97% accuracy with a 2-layer MLP. However, OptuNet has only 392 parameters, a significantly lower number than a comparable MLP: considering a hidden dimension of 10, we would expect at least 7600 parameters, more than 19 times as much as our network.

Reviewer comment (Experiments):
Are you employing data augmentation in these experiments? And relatedly, are you tempering the posteriors, i.e. performing a grid search over temperatures? I’m asking since the cold posterior effect [6] could be a potential confounder here for test performance, as different approximations might be influenced differently.

Author response:
**Regarding the data augmentation [Q2],** we deliberately keep the CIFAR experiments simple, employing only horizontal flips to avoid poisoning the posterior. Indeed, some data augmentations have been shown to sometimes harm ensembles and multi-mode methods (e.g., [**1**]). Finally, we refrain from tempering the posteriors to focus on understanding the relationship between weight-space symmetries and the posterior.

Reviewer comment (Presentation):
The paper seems to lack a specific focus. While the theoretical and experimental parts of the paper are both exciting, they seem largely disconnected. The developed mathematical formalism does not appear to be used for anything, and it is even unclear what these definitions buy us in terms of understanding BNN posteriors. The experiments in section 4 do not appear to consider symmetries at all, and whereas those of section 5 do, the link to the definitions in section 3 is unclear. To me, the paper seems to be compiled from two distinct papers, each of which would be interesting to read.

Author response:
- **Concerning the lack of a clear focus [W1, Q1]:** The primary focus of our paper is to elucidate the impact of weight-space symmetries on the posterior of modern DNNs. We believe that enhancing the understanding of DNNs involves both theoretical and experimental aspects, both of which are encompassed in our work. As such, we believe that our paper is not a compilation of two different papers. Our qualitative results in Figures 1 and 10 (Appendix) illustrate how symmetries can distort the posterior estimation. While these results are not fully conclusively supported by Table 1, the challenges of representing distributions in extremely high-dimensional spaces alter the meaning of the simplest distance metrics. We hypothesize that MMD may address these symmetry issues, potentially obscuring the phenomena we aim to highlight. However, we acknowledge your concerns and will try to add another more explainable metric working directly on the marginals (see also **[Q4]**).

Reviewer comment (Writing):
The clarity of the paper could be improved. The figures (1 and 2 in particular) are not explained in sufficient detail to understand what they show, and the text itself is sometimes unclear.

Author response:
- **Concerning the clarity of figures and MMD [W2, Q2, Q3],** recognizing the need for conciseness, we have chosen what to include in the main paper versus the appendix. We have moved some detailed explanations of Figure 1 to the main paper and provided additional clarification for Figure 2 in Section 3.6. In Figure 2, we provide insights on the difference of mass between 1) the network at the end of the training (that we call at convergence) and 2) the same network after minimization of its regularization term (at the optimum). We are curious about your opinion on whether these changes improve the paper's clarity on these points. Regarding the MMD, we will rephrase this section to emphasize that MMD serves as a suitable discrepancy metric for characterizing distributions when appropriate kernels are chosen and clarify the sentence you highlighted in **[Q3]**.

Reviewer comment (Theory):
What is the link between the formalism of section 3 and the experiments in sections 4 and 5?

Author response:
- **Concerning the clarity of figures and MMD [W2, Q2, Q3],** recognizing the need for conciseness, we have chosen what to include in the main paper versus the appendix. We have moved some detailed explanations of Figure 1 to the main paper and provided additional clarification for Figure 2 in Section 3.6. In Figure 2, we provide insights on the difference of mass between 1) the network at the end of the training (that we call at convergence) and 2) the same network after minimization of its regularization term (at the optimum). We are curious about your opinion on whether these changes improve the paper's clarity on these points. Regarding the MMD, we will rephrase this section to emphasize that MMD serves as a suitable discrepancy metric for characterizing distributions when appropriate kernels are chosen and clarify the sentence you highlighted in **[Q3]**.

Reviewer comment (Presentation):
I don't fully understand figure 2. What is on the second axis in the left plot, what does the middle plot show, and what is the difference between "opt." and "convergence" in the right plot?

Author response:
- **Concerning the clarity of figures and MMD [W2, Q2, Q3],** recognizing the need for conciseness, we have chosen what to include in the main paper versus the appendix. We have moved some detailed explanations of Figure 1 to the main paper and provided additional clarification for Figure 2 in Section 3.6. In Figure 2, we provide insights on the difference of mass between 1) the network at the end of the training (that we call at convergence) and 2) the same network after minimization of its regularization term (at the optimum). We are curious about your opinion on whether these changes improve the paper's clarity on these points. Regarding the MMD, we will rephrase this section to emphasize that MMD serves as a suitable discrepancy metric for characterizing distributions when appropriate kernels are chosen and clarify the sentence you highlighted in **[Q3]**.

Reviewer comment (Writing):
In section 4.1, you write "For better efficacity, MMDs are computed on RKHS that allow for comparing all of their moments." What does this mean?

Author response:
- **Concerning the clarity of figures and MMD [W2, Q2, Q3],** recognizing the need for conciseness, we have chosen what to include in the main paper versus the appendix. We have moved some detailed explanations of Figure 1 to the main paper and provided additional clarification for Figure 2 in Section 3.6. In Figure 2, we provide insights on the difference of mass between 1) the network at the end of the training (that we call at convergence) and 2) the same network after minimization of its regularization term (at the optimum). We are curious about your opinion on whether these changes improve the paper's clarity on these points. Regarding the MMD, we will rephrase this section to emphasize that MMD serves as a suitable discrepancy metric for characterizing distributions when appropriate kernels are chosen and clarify the sentence you highlighted in **[Q3]**.

Reviewer comment (Theory):
If I understand the paper correctly, the estimates of the BNN posteriors come from the parameters of a 1000-member ensemble trained using maximum likelihood. Can we be sure this is a faithful representation of the posterior? For instance, do we know anything about the higher-order moments of those modes?

Author response:
- **Regarding the nature of Ground Truth Posterior [Q4],** we acknowledge the inherent uncertainty in representing the posterior with 1000 DNNs. While we understand this observation, we should have addressed this debate more explicitly in the paper to provide context for new readers. We will add such a discussion in the next update of our submission. However, this nuance should not invalidate our results. Indeed, MMDs compare samples drawn from different distributions and have the advantage of converging very quickly. However, we intend to add at least another distance on the marginals, which will be more interpretable.  

Dear Reviewer **QYDw**,

We are pleased that our discussions with the reviewers were insightful and that you value our work during this rebuttal and the modifications that we have implemented.
We fully agree with you that the limitations of the posterior estimation by DE were not yet transparent enough in the core of our previous version of the manuscript. We now make this limitation more explicit at the end of the introduction of Section 4, just before the pointer to Appendix B. As recommended, we have removed all occurrences of “ground truth,” which we agree were misleading.

We will continue to improve our work, and we thank you again. 

Sincerely, 

The authors

Reviewer comment (Evaluation):
Related to the previous question, if the posterior is indeed approximated by 1000 ML solutions, does the MMD metric even make sense for any of the single-mode methods? One could argue that single-mode methods aren't meant to describe the posterior adequately, but the hope is that their predictive distributions aren't too affected by the single-mode limitation.

Author response:
- **Concerning the utility of Single-Mode Methods [Q5]:** Single-mode strategies are standard in uncertainty quantification, with only a few papers exploring multi-mode approaches. It is crucial to demonstrate the potential issues with single-mode methods, as this contributes to the broader understanding of uncertainty quantification. While we agree that they do not necessarily seek to optimize their estimation of the posterior, we argue that it remains important to test their ability to estimate the epistemic uncertainty properly. We also agree that comparing multi-modal distributions to single-mode distributions can be unfair; however, please keep in mind that all of the single-mode methods have been chosen on the basis that they claim to sample from approximations of the posterior.

Reviewer comment (Experiments):
limited scope in empirical validation: while the dataset released is extensive, the paper's empirical validation primarily focuses on vision tasks and specific architectures like resnet-18. this raises questions about the generalizability of the findings across different types of neural network architectures and tasks. expanding the empirical validation to include a broader range of architectures would strengthen the findings.

Author response:
**Regarding the limited empirical scope of the findings and dataset [W1, Q3, Q6]**, we fully agree with the reviewer on this point. To improve on this side, we intend to enrich our dataset of checkpoints with two other types of models, starting with simple MLPs on regression tasks, as well as LSTMs on a time-series forecasting dataset. We also aim to add a table in the supplementary materials with the results on the MLPs and these LSTMs before the end of the rebuttal. 

More specifically, for [**Q3**], a limitation of our work - at least for the scaling symmetries part - resides in using non-negative homogenous activation functions, such as the ReLU. This may become a problem in vision tasks where the GeLU is starting to take precedence, in ViTs, of course, but also in modern ConvNets such as ResNeXt [**1**] (even though it does not seem to yield better performance). 

One interesting aspect we could consider is the posterior of neural networks after fine-tuning on downstream tasks, either in NLP or vision. This could be more affordable considering the computational cost of training current moderate to large-sized models.