acceptodds
Under review as a conference paper at ICLR 2027

Inference for Transformer Representation Shifts Through Metric Fields

Abstract

How can we determine whether a transformer has undergone a systematic shift in its internal representations? Existing methods typically summarize activations over a fixed collection of inputs, but do not directly quantify whether an observed difference persists across a population of input sequences. We formulate representation-shift detection as a population-level inference problem. Each randomly sampled sequence induces a hidden-state surface over layer depth and token position, which we treat as a random functional object and characterize through its induced metric tensor field. This representation is invariant to fixed global orthogonal transformations while preserving the spatial organization of model representations. Using paired inputs, we define the expected difference between metric fields over a prespecified task distribution as the inferential target and develop a global spectral test for detecting systematic shifts. In a controlled study of continued training, replacing only 1% of the training corpus with data from a different source produces a detection signal more than two orders of magnitude larger than that under the batch-order control. We further introduce a tolerance-based screening rule to distinguish small but detectable departures, such as those arising from uncontrollable noise, from substantively larger representation shifts. Together, these results provide a statistical framework for detecting, quantifying, and spatially characterizing transformer representation shifts at the population level.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Transformer representations, Representation shift, Representation learning, Statistical inference, Functional data analysis, Model monitoring

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_cX2JOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper proposes a theoretically-motivated statistical measure for whether transformer representations have changed over training, and shows that it shows a sensitive measure that detects differences between training corpora, and scales appropriately with the magnitude of those differences.

Critical strengths
  • The proposed measure makes sense
  • The empirical results support the measure detecting what it is intended to
Critical weaknesses
  • My core concern about this work is that it is answering a question that it is unclear if anybody has asked (or wants to). In particular, we are generally concerned about similarities and differences between models for a practical reason — e.g. that we want to know if a model meaningfully improves on another in terms of its accuracy, or if training has had some effect. Those questions seem to be better addressed through explicit behavioral measurements on those domains (or at least, this paper has not validated that the measure tells us anything useful for these kinds of differences). It may often be the case that a detectable difference in representations has no effect on the behaviors we actually care about. The paper does not make a strong case that this measure cleanly detects something we actually care about.

  • The experiments focus on the setting where the probes match the domain(s) that the data changed on (e.g., swapping tinystories for wiki data, and calcuating the metric differences using sequences from both). I struggle to imagine a practical use case, where we would assume we already know which parts of the distribution will have changed (e.g., which data has been swapped out) but this measure would still be useful. It would be thus a much stronger empirical validation to show that estimating the metrics on data from a third non-overlapping domain (e.g., math text, or code, or whatever) would still be able to detect the training differences.

Questions for authors
  • Why should we care about this?
  • Can you demonstrate that it is selectively useful for some practical use case (i.e., it predicts some downstream measure we actually care about)?
  • Can you show that the measure is still sensitive even if you estimate the changes on a different distribution than where the data changed?
3 comments

We thank the reviewer for the careful reading and thoughtful questions. We address the critical concerns as well as other questions in two parts: (i) the practical application of the metric field and (ii) the robustness of the metric field on unseen domains.

i

We agree that we did not make a strong case that this measure tells us anything useful for these kinds of differences. To address this critical weakness, we added an application where the metric field difference obtained during training is used to guide model adaptation. This allows us to use the metric to select a subset of parameters to adapt rather than adapting all parameters. One such application is choosing where to adapt a model under a limited parameter budget while retaining performance on an existing task.

The new experiment tests whether the field helps select an effective adaptation (a patch over layer and token position) under a fixed parameter budget. Both the field-guided and layer-only LoReFT rules use the same amount of trainable parameters. Their new-task accuracies are 81.80% versus 56.80%, 83.08% versus 53.00%, and 79.96% versus 29.36%, yielding gains of 25.00, 30.08, and 50.60 percentage points. The results are put in Table 4 of section 5.4 of the revised manuscript.

ii.

The additional experiment keeps continuation training on TinyStories and WikiText unchanged, but evaluates the resulting checkpoints on code and mathematics prompts. The metric field-based measure is still sensitive to the change in the training data on the unseen domains. The results are put in Table 2 of the revised manuscript. The measures behave similarly to the original results, regardless of the evaluation domains. This addresses the concern that the original results might depend on using prompts from the two training domains.

Thanks to the authors for this response. These additional experiments have mildly improved my impression of the paper, but I think there are still serious issues that would benefit from a more thorough revision and resubmission to a future conference:

i. On layer selection for LoRA, if I understand correctly the full LoRA strictly outperforms your field-based selection on both new task performance (B) and old task retention (A), as shown on task set 1 (since you didn't eval the full lora on 2 and 3)? I don't think you can claim that field-based selection helps if it performs strictly worse than the full LoRA (I guess it uses fewer parameters, but if you want to make that comparison you should compare to stronger baselines like training the lora using only that many parameters / layers, or stronger selection methods like compute matched evals of different layers, etc.)

ii. These experiments are a bit more satisfying, but your response to me here (that evaluation domain doesn't matter) seems to contradict your discussion with the other reviewer above on the two orders of magnitude claim and the domains where it applies? Indeed, the magnitude of the effects on these domains seems much smaller, consistent with the large effects described originally being largely from testing on the changed domain.

Furthermore, these new experiments, as with others in the paper, would benefit from running multiple seeds (e.g., do multiple full loras and multiple selections so we can evaluate the significance of differences w.r.t. the variation within each condition).

We thank the reviewer for the additional assessment and constructive suggestions. We appreciate that the new experiments have improved your assessment, and we hope the following clarifications help address the remaining concerns. We are also conducting additional replications with different random seeds and will report the results if available before the discussion period ends.

(i)

We agree that full LoRA achieves better performance than field-guided adaptation in Task Set 1. However, our objective is not to demonstrate superiority over full LoRA in absolute predictive performance, but to investigate whether the proposed metric field provides useful information for selecting where to adapt under a limited parameter budget.

Importantly, the layer-only baseline already provides a comparison similar to your suggestion. Both the "Layer-only" and "Field Rule" approaches use the same number of trainable parameters. The distinction is that the layer-only baseline applies adaptation uniformly across token positions in the selected layers, whereas the field-guided approach uses the metric field to identify specific layer–token positions for adaptation. The substantial improvements across the three task sets therefore provide evidence that the metric field offers useful information. It can improve adaptation under an identical trainable-parameter budget.

(ii)

We apologize that our previous response did not clearly distinguish between the sensitivity of the measure and the magnitude of the resulting statistic.

Our claim is not that the magnitude of the metric-field difference is invariant across evaluation domains. Rather, the measure remains sensitive to changes in model representations when evaluated on prompts from domains not used for continuation training. While the magnitude varies across evaluation domains, the qualitative conclusion regarding the detection of representational differences remains unchanged in the evaluated settings.

To avoid overstating the generality of our findings, we have already removed the unqualified "two orders of magnitude" statement from the abstract and clarified the scope of the corresponding results. The additional experiments are intended to establish robustness of detection, rather than invariance of effect magnitude, across evaluation domains.

We hope these clarifications better explain the intended contributions

Reviewer_M1GTOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The authors want a principled way to say whether two versions of a language model have changed across a whole population of inputs. For each input, they treat the model’s internal activations as a “surface” over normalized depth and position; this surface is represented by a “metric field” that records how fast those activations are changing with respect to their own coordinate (and a cross-term between the two). Comparing two models then becomes a question about whether the average difference is zero or not. They validate this by forking a trained-from-scratch small model and continuing training with increasing amounts of a second corpus mixed in. They also propose a tolerance knob to ignore shifts that are small.

Critical strengths
  1. The basic setup appears sensible and the training experiment has careful controls. The manuscript frames the overarching question of “did the model change?” as the statistical question: “is the averaged comparison different from zero?” The controls seem clever, particularly the rerun with only GPU randomness, and the rerun with only the data order shuffled. Against those, mixing in just one percent of a new corpus produces a very large signal, which is a genuinely interesting observation.

  2. The quantity measured per input does not depend on how wide the model is or how its internal coordinates happen to be arranged so the same procedure can be applied to models of different sizes. The appendix heat maps give a readable layer-by-layer picture of where instruction tuning and code tuning changed things. These figures are, unfortunately, buried in the appendix.

Critical weaknesses

The headline results, which I interpret as Table 1 and Figs 1-2 are hard to take at face value: In Table1/Fig1 half the test prompts come from the corpus that was mixed in, but the manuscript doesn’t report the metric results separately for the two kinds of prompts, so we cannot tell how the model changed on its original task or only on the new kind of text under the various doses. Additionally: every dose and every control seems to come from a single training run– with no way to judge how reliable or stable this pattern is. The reported metric says two models differ but not whether the difference matters since the test flags any two models that are not byte-identical, including two runs that differ only by GPU randomness. The tolerance knob meant to fix this has no natural scale across representations and no guidance for setting it.

I was admittedly not able to follow the mathematical sections entirely– but I am not sure I understand even the intuition behind the derivative with respect to the token position. My intuition is that the differences between subsequent token window average representations has no well-motivated reason to depend on the progress through the context window– even if it can be made smooth enough to motivate a derivative by the averaging (I do see how that this kind of derivative can be well motivated through the layers). Somewhat supporting this point: the part of the metric that looks along the token sequence direction shows very little structure in figure 4.

Questions for authors
  • Would the authors consider changing table 1 into a figure and showing results separately for the TinyStories prompts and the WikiText prompts? Does the large signal appear on the TinyStories prompts? Does the change detected on those prompts predict anything about the model’s behavior on that data, such as loss or output changes?
  • Every dose and control is one training run. Could you run the shuffled-order control several times so we can see how much it varies on its own?
  • What does “population-level” give you that people do not already get by resampling their inputs when computing, for example, CKA?
  • The tolerance Δ has no inherent scale, and flags GPU randomness at 0. How should someone choose a value?
  • What does the size of the measure differences in model geometry mean? Figure 1b might be read as suggesting the metric is insensitive to the size of the difference: is that a fair characterization? Can you give an example of a change to the model that the measurement would miss?
  • What is the token-position component supposed to capture? In Figure 4 it is almost flat along that axis. Would single dimensional per-layer number carry essentially the same information?
  • The null distribution drops five percent of its mass by truncation: does using all eigenvalues change any conclusions?
  • How does treating layers and positions as continuous coordinates buy anything in the current study? All computation is on a fixed grid, and I did not find comparisons between models with different numbers of layers.
  • What is meant by “continuation fraction h/H” in the Figure 1 caption?
  • The first token in a sequence can often have enormous activations. Was it excluded when averaging? If not, does it dominate the patterns you see when included in an averaging bin?
4 comments

\We thank the reviewer for the careful reading and for the detailed questions.

CW1. Thank you for raising the concern about the headline results. We have included experiments that evaluate on new domains (Table 2 in the revised manuscript) rather than domains that are used in the training. We will run more repetitions so that the reported numbers will have a variance measure to describe the stability of the results. Yes, we agree with the reviewer that the tolerance should be chosen carefully, like a hyperparameter. We have added a discussion on how to choose the tolerance in the appendix (Section F) of the revised manuscript.

CW2. Thank you for the question. The main motivation is to allow the token and layer to vary when we are doing model comparisons. The current examples use varying token lengths. We have conducted additional experiments to compare models with different numbers of layers in Table 3 of the revised manuscript.

We will address your concern on the spatial pattern in question 6 together in the following.

In a new experiment (Table 4 in Section 5.4), we use this token position to guide LoReFT adaptation. This allows better accuracy for the fine-tuning process rather than adapting all parameters given the same parameter budget.

Q1. We have repeated the experiments but evaluated on new domains (Math and Code) rather than domains that are used in the training. The results are presented in Table 2 of the revised manuscript. The results are consistent w.r.t. evaluation on TinyStories prompts. This shows the robustness of the metric field on the unseen domains.

We did not directly try to link the metric field difference to the model performance difference. However, we have added a new experiment (Table 4 in Section 5.4) where we use the metric field to guide LoReFT adaptation.

Q2. We are running more repetitions of the experiments so the reported numbers will have a variance measure to describe the stability of the results.

Q3. The population-level gives us the foundation for doing statistical inferences, like confidence intervals and hypothesis testing. This is more than doing resampling on the input data.

Q4. We have added a discussion on how to choose the tolerance in the appendix (Section F) of the revised manuscript. The idea is to control how many times (through a probability) we falsely flag the C2 control as significant.

Q5. Old Figure 1(b) only suggests the monotonicity of the metric field difference given an increasing portion of mixed training data. It is sensitive to the size of the difference, and we have the raw numbers in Table 1. The bar heights may be misleading due to the different scales of the metrics. We will remove (and put in the appendix) panel (b) from Figure 1 and replace it with one comparing models with different numbers of layers.

For example, consider a model that is repeatedly fine-tuned on duplicated training sequences. The model may increasingly memorize these sequences, changing its next-token probabilities without changing any intermediate hidden states. Consequently, the induced metric field remains exactly unchanged, and our test cannot detect this behavioral shift. More generally, the metric is invariant to fixed global orthogonal transformations of hidden representations, even when their coordinates change substantially.

Q6. The token-position component measures how the direction of the binned hidden-state representation changes across neighboring relative positions within a prompt. Being flat means the rate of change is the same across the token positions, but it does not mean the representation is not changing.

The follow-up experiment in Table 4 is to compare layer-wise or patch-wise adaptation, where the latter is our proposed method and the former is what you mentioned. The results suggest that patch-wise adaptation is significantly better than just using a single-dimensional per-layer number.

Q7. We thank the reviewer for raising this calibration issue. We clarify that the 95% truncation criterion retains at least 95% of the total empirical covariance variance, rather than 95% of the probability mass of the limiting null distribution. We agree that retaining 95% of the variance does not automatically guarantee a negligible approximation error. In addition, this is a technique used to deal with functional data, which are inherently infinite-dimensional and need truncation.

Q8. We have added new applications (Table 3) where we compare models with different numbers of layers.

Q9. (h) is the current continuation step and (H=1,000) is the planned continuation length. Thus, a value of 0.5 corresponds to 500 updates after the common fork.

Q10. The first token is not excluded. We use normalization to make the hidden states unit-norm. The metric field focuses on the relative changes rather than the absolute changes.

I appreciate the authors thorough response, and the significant effort in the revision.

I am currently keeping my assessment as is, due to a couple of issues that, if sufficiently addressed, would alter my recommendation.

First. In light of the new results on math and code, the abstract currently reads to me as somewhat misleading. the two orders of magnitude disappeared under the swap to math/code. While it is true that there is a study in which 2 orders of magnitude is accurate-- it does not seem to describe the full results fairly anymore. I am also curious about the authors choice to not separate the TinyStories prompts and the WikiText prompts in table 1. Separation of the two may also reveal that the lion's share of the two orders of magnitude came from WikiText and not TinyStories. How would this affect the significance of the results, if true?

Second. In addressing one of my other primary concerns (the importance of the context position resolution), the authors chose to refer to some new experiment in table 4. I am not entirely sure what the right apples to apples comparison is. The layer only approach seems to have significantly more context positions to fit the LoReFT to, but only has the same number of parameters to do it. Perhaps using something else (but NOT the metric) to select the same number of context positions for the "layer only" case would be a better control. Picking the token positions uniformly across the context might serve as a good control? Not knowing the details of the retrieval task makes it a bit hard to know. I think a fairly standard approach would be to select the beginning and end of the prompt as good positions, which might be a somewhat more well-motivated baseline than the uniform test.

Related: do the results in table 1/2 differ much if you use a context-position averaged version of the metric.

We thank the reviewer again for reading our revised manuscript and providing insightful comments. We agree that our previous presentation needed a clearer qualification of the evaluation domain and a more controlled comparison of context-position selection. We have expanded Tables 1, 2, and 4 to address these points. In addition, we will address these concerns by C1, C2, C3 in the following.

C1.

We have removed the “two orders of magnitude” statement from the abstract and separated the TinyStories and WikiText prompts in Table 1. The separated results support your concern: at 1% corpus substitution, the control-normalized statistic is 185 on WikiText but only 1.34 on TinyStories, compared with 184 in the pooled evaluation. This finding suggests that we have to specify the evaluation population rather than making a generalized claim.

Nonetheless, this result does not change the conclusion of the paper. The metric field is still sensitive and monotonic to changes in the training data, assuming we don't know the label of the training data. This does not change other applications of the metric field.

C2.

Thank you for pointing this out. We have added new strategies for selecting token windows to do the LoReFT adaptation, including your suggestion of selecting the beginning and end of the prompt. The results are presented in Table 4 of the revised manuscript. When we are not using the metric field to select token windows, the performance is significantly worse than when using the metric field. This suggests that, under a fixed domain, there might be some optimal token windows that are more dominant for the model to learn. In addition, we have specified that task A is a one-hop retrieval task and task B is a two-hop retrieval task.

C3.

Thank you for the suggestion. We have added a new experiment to compare the metric field with the context-position averaged version of the metric. The results are put in Tables 1 and 2 as an extra row in the table. It works similarly to other scale-valued metrics, but not on the same magnitude as the metric field. The full metric field has a larger control-normalized statistic in comparisons across all domains. Thus, position averaging retains some response to representation changes, but having an additional argument (dimension in the functional object) provides greater insights. The difference could be the difference between using a univariate (removed token t from averaging) and bivariate functional object (the metric field).

Thanks for running these extra tests.

My concern about the context position component of the metric seems to have been resolved (and in your favor!)

I still feel that the additional tests that show the metric sensitivity on WikiText only, along with the discussion of reviewer cX2J warrants some limiting of the claims.

For example, the original claim of 1% fine-tune giving a 2 order magnitude increase in sensitivity over the baseline. The two order of magnitude has been reduced to 1 order of magnitude. The 1% claim also should be limited now, in light of these results.

The entire claim needs renewed scrutiny from the authors at this point, to make sure it is in line with the numerical evidence. On a positive note, the authors did provide a use case for their metric-- which can be thought of as an additional contribution. THis offsets the weakening of the original claim.

I will upgrade my score from a 2->3, conditioned on the authors agreeing to refine their claims to match the evidence (the limits of the sensitivity of the metric when it comes to training dose and domain need to be made clear).

I also agree with reviewer cXJ2 that more seeds and variability would make the paper stronger-- if the authors have access to the compute, I suggest doing this.

Reviewer_pNuuOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The motivation for the paper is that existing methods for comparing internal representations depend on a fixed set of inputs, which is a sample from a larger population. However, many of these methods lack a way to quantify uncertainty coming from sampling variability. Given a fixed prompt, the authors propose to compute the induced metric field, and then define geometric change as the expected metric-field difference. They define a procedure for how to determine whether a representation shift is significant. They evaluate their method by comparing Qwen2.5-0.5B models that, starting from a common checkpoint (trained from scratch on TinyStories), are trained using different proportion of continuation-training data drawn from a second corpus (WikiText-103).

Critical strengths
  • The paper is well-organized, the contributions are clearly articulated, and the motivation is clear.
  • The method is principled and explained well, and Appendix B contains helpful details which answered some of the questions I had from the main body of the paper.
Critical weaknesses
  • Section 5 (Experiments) lacks interpretation in places. For example:
    • Several other similarity measures in Table 1 also increase monotonically with the mixture dose rho. While g has larger (value/C2) ratios it is not clear to me from the information provided if that translates into better detection performance compared to the methods that also have relatively large ratios?
    • Figure 1 (right) shows that KL changes more across mixture proportions compared to g. Can g distinguish the models trained on different mixture proportions rho? (Is this an intended use of g?)

More questions about Section 5 are in the Questions For Authors section below.

  • In several places early in the paper the authors discuss being able to analyze the spatial pattern as a benefit of the method: (Line 134-135: "We test whether the expected metric-field difference is zero and report its spatial pattern." Line 283: "When the global null is rejected, the estimated mean field D_n^c(u) can be inspected to characterize the spatial organization of the detected shift.") However, I don't think there are experimental results about this in the main text, and Figure 4 in Appendix C receives little interpretation.
    • Another reason I think this is important is that in Related Work it says "The proposed framework is therefore not another scalar valued measure for similarity in representations", but then the main experiments seem to emphasize the scalar value measure over the framework.
Questions for authors

Questions for the authors

Section 5

  • Figure 1: "The temporal trajectories differ by substitution dose: lower-dose branches generally decline over the observed continuation window, whereas the largest-dose branch increases later in training" what is the intuition for this? Is there an explanation that could be provided?
  • Could you add information about how long it took to compute the metric g compared to the other metrics in the table?
  • There should be no difference with C0, but could these results be reported in the main text?
  • I was surprised by the magnitude of T_{n, obs}. Is this surprising, is there intuition you can offer for this?
  • It should be more clear that ||\Delta(W)||(Zhong and Raghunathan) in Table 1 is not their method (Line 1063: "Weight drift (data free, since the activation-response component of that method requires additional formard passes and is not computed).") While this is stated in Appendix D, I think it should also be stated in Section 5, or perhaps the citation (Zhong and Raghunathan) could be removed to prevent confusion.

Other suggestions

  • The related work section might be more helpful after your method is explained/introduced.
  • If you have examples of representation changes that the method fails to detect could you include this in the Appendix? This would be helpful for potential users of the method!

Minor comments

  • The sentence "The limiting null distribution is therefore a weighted chi-square mixture." is repreated twice in short succession: line 282 and line 295.
  • Line 680: "More details are given in Appendix B" (This is already Appendix B)
2 comments

We thank the reviewer for the careful reading and for the detailed questions.

CW1. Thank you for the comment. We agree that a larger ratio relative to the C2 control does not necessarily imply superior detection power. Table 1 is intended to characterize the empirical response to increasing mixture doses rather than establish a formal ranking of detection power. The comparison also allows us to assess whether its behavior is consistent with established similarity measures.

More importantly, our contribution extends beyond introducing another similarity measure. Our main goal is to introduce a metric field that preserves the spatial organization of representation shifts. In the meantime, this field is a random and statistical object that supports inference as well as allowing further interpretation and practical applications.

First, we have added new experiments to evaluate the inferential procedure on domains that are not used in the training. The results are put in the section 5.1 of the main text, where they do agree with the previous results. Second, the reason why we introduce this field over similarity measures is that it offers a natural way to compare models with different numbers of layers or different binning or token input lengths. Previous experiments focused on varying token length, and we have added experiments in Section 5.3 to compare models with different numbers of layers. Furthermore, we have added a new application where we use the estimated field to select layers and token positions for model adaptation. The results are put in section 5.4 of the main text. We were able to select a subset of parameters to adapt rather than adapting all parameters during fine-tuning. Also, carefully selecting token positions to adapt is more beneficial than ignoring token information, as illustrated in the new experiment.

CW2. We thank the reviewer for the careful observation. The primary objective of our framework is to detect and characterize systematic differences in representation geometry between specified models, rather than identify the training mixture proportion (ρ\rho). Figure 1(b) (now in the appendix) shows that the metric-field statistic increases monotonically across the six substitution doses, from 184 to 557 times the batch-order control. However, these statistics compare each treatment against the common (ρ=0\rho=0) reference. Their ordering provides descriptive evidence of a dose response but does not establish that models trained at different nonzero proportions have statistically distinguishable metric fields. KL may exhibit a steeper dose response while measuring output-level rather than internal geometric differences.

CW3. We thank the reviewer for the suggestion. Due to the page limit, we focused more on the main contributions and the experimental results rather than the interpretation of metric fields. We have added some interpretation of the spatial pattern in the appendix.

Q1. We thank the reviewer for this question. Figure 1(a) measures the geometric discrepancy between two simultaneously evolving checkpoints, rather than each model's departure from the common initialization M⋆M^\star. Consequently, the statistic need not increase monotonically with training time. At smaller substitution doses, both branches continue training predominantly on TinyStories, sharing most training examples and the same underlying objective. Differences introduced by the substituted WikiText batches may therefore be mitigated by subsequent updates on shared data, explaining the modest decline in geometric discrepancy. Importantly, this does not imply that either model returns toward its initial representation. At the largest dose (ρ=1\rho=1), the treatment branch trains entirely on WikiText while the reference continues on TinyStories. Their different training objectives may produce increasingly distinct representations, explaining the later increase in discrepancy.We have removed C2 and the control from Figure 1, so it's easier to see the difference between different doses of ρ\rho.

Q2. We thank the reviewer for the question. We agree that computational cost is necessary for assessing practical use. Our current results do not include a matched runtime comparison, since it's not a priority for the current study.

Q3. We thank the reviewer for this careful observation. Yes, there should be no difference with C0, and our saved results show this.

Q4. We thank the reviewer for this question. The large numerical values of the statistic are not surprising. It equals the sample size multiplied by the squared mean-field norm, (Tn=n∣Dˉn∣H2)(T_n=n\\|\bar{D}_n\\|_{\mathcal{H}}^{2}), and is not bounded between zero and one. Statistical interpretation therefore depends on the corresponding covariance-based null distribution, not the actual value of the statistic.

Q5. We thank the reviewer for this clarification. We have removed the citation and comparison from the work.

Thank you to the authors for their revisions and detailed responses to my questions. I will keep my score.

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