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Under review as a conference paper at ICLR 2027

Probing Under Distribution Shift: Learning Generalizable Distributed Representations of LLM Activations

Abstract

Probing is one of the most promising approaches for monitoring the internal states of large language models: probes read a subset of model activations and predict an external variable of interest. Yet recent work has documented poor out-of-distribution generalization, overfitting. These are standard supervised-learning generalization problems, of which probing is a special case, with the additional challenge that its inputs come from the high-dimensional and highly structured activation space of a pretrained model. Therefore, we propose to focus on generalization and evaluate probes under distribution shift using **leave-one-environment-out evaluation**. This perspective suggests two natural independent methodological directions: distributionally robust learning that explicitly targets generalization across environments, and learning distributed representations of the activation space that best support generalizable predictions. We systematically compare baseline probes with distributed representations trained with and without distributionally robust objectives. Across three tasks and 15 environments, our proposed distributed representations consistently improve OOD generalization despite greater complexity, while none of the existing distributionally robust methods we evaluate provides additional gains. Our proposed distributed representation compresses the full activation tensor via two-stage inducing-point attention with a sparse layer selector, meaning that once it is learned the probe remain resource-efficient. Our results suggest that regularization is better achieved by training across diverse environments than by simply constraining probe complexity. Finally, we discuss implication for future research.

Primary area:
interpretability and explainable AI
Keywords:
probing, large language models, out-of-distribution generalization, distributed representations, activation monitoring, robustness

Reviews

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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_U6VNOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

This paper studies the out-of-distribution (OOD) generalization of probes trained on LLM activations. The authors propose Factorized Axial Latent Attention (FALA), which learns distributed representations by aggregating activations across layers and token positions through two-stage cross-attention, together with sparse layer selection to reduce overfitting. Experiments on three probing tasks—hallucination detection, uncertainty calibration, and training-data familiarity—show that the proposed method improves OOD generalization over conventional probing baselines, particularly for uncertainty calibration. The authors also evaluate several distributionally robust learning methods and find that none consistently outperforms standard empirical risk minimization (ERM). Further experiments suggest that increasing the diversity of training environments is more beneficial than simply adding samples from existing environments.

Critical strengths

Comprehensive experimental evaluation. The authors evaluate probing methods across three tasks and 15 environments, comparing different distributed representation architectures and a broad range of distributionally robust learning objectives. The experiments also include several baselines and ablations.

Critical weaknesses
  1. Limited improvements over existing baselines. Although FALA-G achieves substantial improvements on uncertainty calibration (S2), its advantages on hallucination detection (S1) and training-data familiarity (S3) are limited. On S1, FALA-G achieves nearly identical average AUROC to the mean-token baseline (0.776 vs. 0.777). On S3, FALA-G achieves only a modest improvement over mean-token pooling (0.702 vs. 0.676) and even performs slightly worse than the random-initialization control (0.702 vs. 0.714). These results weaken the claim that the proposed architecture consistently improves OOD generalization.

  2. Limited methodological novelty. FALA primarily combines existing architectural components, including inducing-point cross-attention, axial attention, and Gumbel-based sparse layer selection. While their application to distributed LLM probing is reasonable, the proposed method introduces limited methodological novelty beyond these established techniques.

  3. Limited insights into OOD generalization. Although the authors conduct extensive experiments, the findings provide limited new understanding of why certain probing architectures generalize better under distribution shift. In particular, the observation that distributionally robust objectives fail to consistently outperform ERM is not accompanied by a sufficiently convincing explanation. Although the representation diagnostics suggest that ERM learns relatively invariant predictors, they do not establish that this invariance explains the lack of additional benefits from distributionally robust objectives.

  4. Missing ablation on sparse layer selection. The authors demonstrate that Gumbel-based sparse layer selection substantially improves performance, but do not compare it against simpler alternatives, such as selecting a fixed subset of layers throughout training or using deterministic top-KK selection without Gumbel noise. Such comparisons would help clarify whether the improvements come from sparsity itself or from the proposed stochastic selection mechanism.

Questions for authors

How does the relative performance of ERM and distributionally robust learning objectives change as the number of available training environments decreases? In particular, could robust objectives become more beneficial when training-environment diversity is limited?

2 comments

Response to Reviewer 3 (Reviewer U6VN) (1/2)

We thank the reviewer for their detailed assessment and for recognizing the breadth of our experimental evaluation. We address each concern below.

1. Limited improvement on S1 and S3

We agree that the improvements on S1 and S3 are smaller than those observed on S2, and we have revised our claims accordingly. In particular, the additional multi-seed experiments show that the differences on S3 are not statistically significant.

Nevertheless, FALA-G remains clearly the best overall choice: it achieves the best performance or performs comparably to the strongest baseline across all three signals, whereas the competing approaches exhibit more pronounced weaknesses on particular tasks. Its main advantage is therefore not a uniformly large improvement on every signal, but consistently competitive performance across substantially different probing problems and distribution shifts.

More importantly, our paper's contribution extends beyond the introduction of FALA-G. We investigate the broader problem of out-of-distribution generalization in activation probing through a systematic LOO evaluation spanning multiple environments, signals, probing architectures, and training objectives. In particular, we believe that our negative findings concerning distributionally robust training constitute an important contribution. Such methods are a natural candidate for addressing generalization failures in probing, yet our extensive evaluation shows that they do not deliver consistent improvements in this setting.

2. Limited methodological novelty

We agree that the individual building blocks of FALA (inducing-point cross-attention, axial factorization, and Gumbel top-K selection) are established techniques. Our methodological contribution lies in their combination for activation probing, but the main contribution is the empirical insight into which aspects of the activation tensor are most useful for cross-environment generalization.

Our experiments indicate that restricting the probe to a sparse subset of layers can be particularly effective. On S2, introducing Gumbel-based sparse selection substantially improves coverage for both FALA and WAP. On the challenging MNLI cross-task evaluation, learning which layers to select with Gumbel noise also outperforms simpler sparse-selection alternatives.

The new ACT-ViT comparison provides further support for this interpretation. Despite processing the full layer × token tensor with approximately three times as many parameters, ACT-ViT does not outperform FALA-G. This suggests that simply exposing the probe to more of the model's internal computation is insufficient; the way this information is selected and aggregated plays a crucial role.

Finally, we emphasize that FALA is only one component of our work. Our broader objective is to characterize OOD generalization in activation probing, including the effects of architecture, activation access, and distributionally robust training. We believe these empirical findings are valuable independently of the novelty of any individual architectural component.

AuthorsOpenReview ↗

Response to Reviewer 3 (Reviewer U6VN) (2/2)

3. Limited insight into why some probing architectures generalize better

We agree that understanding the mechanisms underlying probe generalization is important. Although our experiments cannot provide a complete explanation, they offer several complementary insights.

Where the gain comes from. First, the clearest evidence concerns the role of sparse layer selection. Removing Gumbel-based selection reduces coverage on S2 by more than half for both architectures: from 0.468 to 0.224 for FALA, and from 0.153 to 0.073 for WAP.

Second, simply increasing access to hidden representations does not appear sufficient. ACT-ViT processes the entire layer × token tensor with 2.9 times as many parameters, yet performs worse than FALA-G on S2 and on the cross-task MNLI evaluation. Similarly, concatenating all layers yields a Cov80 of only 0.004 on S2.

Together, these results suggest that the benefit of FALA-G comes at least partly from restricting the information available to the probe, rather than maximizing its access to the model's internal states.

More broadly, we explore an important trade-off in activation probing: increasing the amount of accessible internal computation can make more sophisticated predictive strategies available, but can also increase the difficulty of learning these strategies. A standard linear probe occupies one end of this spectrum: its restricted access and low complexity make it relatively easy to train. At the other extreme, architectures such as ACT-ViT access much richer representations, potentially allowing more expressive prediction strategies, but also creating more opportunities to exploit environment-specific (spurious) correlations. FALA-G offers an intermediate approach: it can aggregate information across tokens and layers but restricted to a learned subset. We hypothesize that this balance between expressive access and structural restriction contributes to its generalization performance.

We do not claim that this provides a complete account of OOD generalization in probing, but we believe the experiments identify a meaningful architectural trade-off and offer concrete evidence for the benefits of selective activation access.

4. Missing ablation on sparse layer selection

We thank the reviewer for this suggestion. We have conducted both requested ablations across all seven evaluation folds (Appendix L):

  • Fixed layers: We replace the learned Gumbel selector with a fixed, contiguous window of layers, selected through a separate linear-probe validation scan. The selected layers are [13, 14, 15] for S1/S2 and [29, 30, 31] for S3, and remain fixed throughout training.
  • Deterministic selection: We retain the learned selector but remove Gumbel noise, using deterministic top-K selection instead.

For the S1 and S2 configurations exhibiting the largest differences in the initial experiments, we additionally evaluated two more random seeds.

On S1 with MNLI, averaged across three seeds, FALA-G achieves an AUROC of 0.675, compared with 0.624 for fixed layers and 0.605 for deterministic selection. These differences correspond to 2.4 and 1.8 standard deviations, respectively. Both alternatives perform at or below the linear-probe baseline (0.625), and every FALA-G seed outperforms every seed of either alternative. Thus, on this particularly challenging distribution shift, merely restricting the probe to a few layers is insufficient: learning which layers to select, with Gumbel noise, provides an additional benefit.

On S2, the results point to a somewhat different conclusion: sparsity itself appears to account for most of the improvement. Both sparse alternatives achieve performance close to FALA-G, whereas removing sparse selection all together reduces Cov80 from 0.468 to 0.224. On S1 NQ and CoQA, the single-seed differences between selection strategies are small (at most 0.014).

On S3, the results are mixed. Given the substantial training variability identified in our multi-seed experiments, we refrain from drawing strong conclusions from these differences.

We have incorporated these results and their interpretation into Appendix L.

Question: Does training-environment diversity matter more when it is scarce?

We are running an additional experiment to test this directly, varying environment diversity while comparing ERM against robust objectives, and will post the results as a follow-up comment if they are ready before the end of the discussion period.

Reviewer_oQueOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper investigates how probes of LLM activations generalize to unseen environments across hallucination detection, uncertainty calibration, and training-data familiarity. It introduces FALA, which combines information across tokens and layers using two-stage attention and sparse layer selection.

Critical strengths
  1. The problem of looking at the robustness of a probe under distribution shift is an important and understudied problem in the OOD generalisation literature. It can present novel kinds of challenges which are perhaps not as common in traditional domains like vision and language where robustness to distribution shift is studied.

  2. The experiment on diversity, i.e., using the same sample budget from one vs a diversity of environments, is quite useful as it identifies domains where labelling effort needs to be allocated.

  3. The paper reports several helpful negative results such as a variety of robustness objectives not all of which necessarily improve performance. This sort of transparent reporting is a good practice.

Critical weaknesses
  1. Close competitors like ACT-ViT are cited but not compared with.

  2. Most results are single-seed. The reported error bars are bootstrap intervals over the test set, which capture sampling noise but not training variance. Given the substantial seed variability acknowledged in the appendix, many of the reported differences may be within run-to-run variation; evaluation across multiple training seeds is needed to establish their reliability.

  3. In section 5.1, the authors claim that their FALA-G is significantly above random init on all signals including S3. However, table 14 shows the AUROC of random init to be 0.714 and that of FAGA-G to be 0.702. Additionally, some of the key empirical results, such as Table 14, appear in the appendix, which makes the main text hard to follow.

  4. Can prior knowledge about the architecture being probed help in better probe design; meaning, can inductive biases be used for robust probe design in this setting? For instance, there are prior works on neural functionals [a] and GNNs [b] that take as input neural networks and predict their various properties. A discussion on the relationship of this work to such literature is important since there are close similarities.

  5. There is no strong justification for why specifically three layers are chosen for regularisation by limiting activation access beyond just reported hyperparameter sweep.

References:

[a] Zhou et al., "Permutation Equivariant Neural Functionals", NeurIPS 2023.
[b] Kofinas et al., "Graph Neural Networks for Learning Equivariant Representations of Neural Networks", ICLR 2024.

Questions for authors

Refer to the weaknesses section.

2 comments

Response to Reviewer 2 (Reviewer oQue) (1/2)

We thank the reviewer for their careful reading, for recognizing probe robustness under distribution shift as an important problem, and for appreciating the breadth of our evaluation across environments and robustness objectives. We address each concern below.

1. ACT-ViT is cited but not compared

Please see our response to Reviewer 1, W1, where we report new multi-seed comparisons with ACT-ViT across all three signals and 15 environments.

2. Single-seed results; bootstrap confidence intervals capture sampling noise rather than training variability

Please see our response to Reviewer 1, W2. We have conducted additional multi-seed experiments and revised our conclusions where training variability prevents a reliable ranking of methods.

3.1 The claim that FALA-G outperforms random initialization on every signal contradicts Table 14

The reviewer is correct. This claim holds for S1 and S2 but not S3, and we have corrected the text accordingly.

Importantly, S3 differs fundamentally from the other signals. For S1 and S2, labels describe the trained model's own behavior, which is disrupted by randomizing its weights. In contrast, S3 concerns an input property: whether a passage appeared in the pretraining corpus. Seen and unseen texts may differ systematically in surface statistics such as vocabulary, formatting, or length. A randomly initialized network can preserve these differences, allowing a probe to distinguish the classes without relying on learned representations.

Thus, random initialization serves as a control for information already extractable from the inputs, independently of the model's learned representations. It does not directly assess the relative merits of probing architectures: all probing methods ACT-ViT, FALA, WAP, or a linear probe can be trained on both trained and randomized networks. Therefore, performance over randomly initialized networks does not speak to weaknesses (or strength) of FALA-G (or any other probing architecture). We have clarified this distinction in Section 4.2 and Appendix G of the revised manuscript.

3.2 Key results are relegated to the appendix, making the main text difficult to follow

Thank you for the comment, we try to improve the presentation. Figure 1 already summarizes the results for all three signals, with the corresponding numerical results reported in Tables 12-14. To make these findings more accessible, we have redesigned Figure 1 into two rows, with non-overlapping markers to improve readability, and added explicit references in the main text to the detailed tables for each signal.

We recognize that some additional results would also benefit from being presented in the main paper. Given the current page limit, we have prioritized an accessible overview of the main findings while retaining the detailed numerical comparisons in the appendix. With the additional space available in the camera-ready version, we intend to move selected supporting results into the main text.

AuthorsOpenReview ↗

Response to Reviewer 2 (Reviewer oQue) (2/2)

4. Missing related work on neural functionals and GNNs over neural networks

We thank the reviewer for bringing Zhou et al. (NeurIPS 2023) and Kofinas et al. (ICLR 2024) to our attention. We have added a discussion of these works. These methods operate on network weights, using architectures designed to respect symmetries such as neuron-permutation equivariance, whereas our work investigates probes operating on the activations of a frozen network.

Nevertheless, we agree that this line of research offers valuable insights for designing more data-efficient and generalizable probing architectures in the future. In particular, structural inductive biases developed in graph neural networks and geometric deep learning could be incorporated into newly developed variants of FALA-G to better exploit known properties of neural representations.

We now discuss this promising direction for future research in Section 6 of the revised manuscript.

5. Insufficient justification for limiting activation access to K = 3 layers

We would like to clarify that K is a hyperparameter of our approach, rather than an intrinsic architectural constraint; we have revised Section 3.1.3 to state this explicitly. There are two parts to this question: why limit access at all, and why K=3 specifically.

Why limit at all. With the Gumbel selector turned off and all 33 layers accessible on the same FALA host (results in Tables 12–14, Appendix G), performance drops by 0.078 AUROC on S1 and 0.245 Cov80 on S2; every fold on both signals moves the same way. On S3, restricting to a learned subset of layers is net positive (mean AUROC +0.104). We attribute this to the data regime: access to all 33 layers increases the effective input dimensionality the attention must aggregate over, and at these label budgets this acts against generalization.

Why K=3. In our experiments, we deliberately adopted a conservative hyperparameter-selection strategy to avoid overestimating the effectiveness of FALA and WAP through extensive task-specific tuning. Specifically, we selected K through a validation sweep over K ∈ {2, …, 6} on a single S1 fold and subsequently kept this value fixed across all three signals, two probing architectures, and two base models.

This choice is important for interpreting the results: we could have optimized K independently for each signal, fold, or architecture, potentially obtaining stronger performance. Instead, we chose to evaluate the generalization of a single configuration across the full experimental setting.

Moreover, selecting only a small number of layers has a practical advantage: it reduces the amount of activation information processed by the probe, yielding a more efficient probe.

In practical applications, researchers using FALA-G to monitor or analyze their own models can naturally treat K as a tunable hyperparameter and optimize it on an appropriate validation set, depending on their computational budget and performance requirements.

Reviewer_HbRzOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
3(+1)
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Paper summary

The authors argue that probes for monitoring the internal states of LLMs should be evaluated based on how well they generalise to data distributions that are unseen. Hence, the authors adopt a leave-one-out protocol, training on various environments except for one and evaluating on that environment left-out. The authors examine two architectures for aggregating information across the layers and tokens of LLM activations: WAP uses learned weighted averages and FALA compresses activations with two stages of attention over learned inducing points, first across layers and then across tokens. The authors also introduce Gumbel-sparse variants that learn a fixed set of three layers to be used at inference.

The paper presents evaluations of these probes on three tasks across 15 task-environments: Detecting Hallucination (S1), Uncertainty Calibration (S2), and Detecting Training-Data Familiarity (S3). The authors demonstrate gains over linear probes under distribution shift, especially for the Gumbel-sparse variants, while none of the seven alternative robust training objectives consistently beat the standard ERM. They also find that adding new training environments can help more than adding more data from existing ones.

Critical strengths
  1. The paper tackles the important problem of the reliability of LLM activation probes under distribution shift. The paper evaluates the proposed methods across three signals and two model families using a leave-one-environment-out protocol. The paper also includes multiple useful controls, such as a probe on a randomly initialised model and a parameter-matched MLP, and also compares matched ERM runs against seven robust training objectives.
  2. The Gumbel-sparse variants provide improvements over their dense counterparts on all three signals. For example, the authors report an AUROC improvement of 0.697 to 0.776 for FALA -> FALA-G on S1, Cov80 improvement of 0.224 to 0.468 on S2, and AUROC improvement of 0.598 to 0.702 on S3. The results are consistent with layer selection acting as a regulariser.
Critical weaknesses
  1. The authors reference ACT-ViT (Bar-Shalom et al., NeurIPS 2025) as an alternative method that learns from (full layer x token) activation tensors, but do not compare against it. This omission conceals whether the proposed aggregation mechanisms in FALA and WAP, and the sparse layer selection introduced in their Gumbel-sparse variants provide an advantage over other methods that learn from full layer x token activation tensors.
  2. Variability across training runs could be more strongly quantified. Some performance gains throughout the paper are marginal as acknowledged by the authors (Section 5.1), and thus having matched multi-seed evals would help establish whether presented improvements are robust against training stochasticity. The main results of Figure 1 and Appendix G showcase bootstrap confidence intervals over test examples, which the authors acknowledge captures sampling rather than training variation. This is relevant for S1, where FALA-G improves mean AUROC over the last-token linear probe by just 0.017 and also does not outperform mean-token pooling (Table 12).
Questions for authors
  1. Can you provide a direct performance comparison against ACT-ViT (Bar-Shalom et al., NeurIPS 2025)? If not feasible, can you provide and mention in the paper, a well-reasoned justification (preferably with empirical evidence referenced) for why the aggregation mechanisms and sparse layer selection of FALA/WAP (and their Gumbel-sparse variants) should offer advantages over ACT-ViT?
  2. Can you provide matched multi-seed evaluations for the main architectural comparisons in Figure 1 and Tables 12-14? If not, how confident are the authors that any suggested improvements are robust to training stochasticity (please provide well-reasoned justification preferably with empirical evidence referenced)?
3 comments

Response to Reviewer 1 (Reviewer HbRz)

We thank the reviewer for their thoughtful assessment, for recognizing the importance of activation-probe reliability under distribution shift, and for acknowledging the improvements obtained by our Gumbel-sparse variants. We address the two weaknesses below.

W1 (and Q1). Missing comparison with ACT-ViT

We agree that ACT-ViT is a relevant baseline and have added it to our experiments. Specifically, we evaluated ACT-ViT using our LOO protocol across all 15 environments and three signals, with multiple random seeds. We also extended our multi-seed evaluation to the other baselines and our proposed methods (see W2).

The new results show that ACT-ViT does not outperform FALA-G on any of the three signals, despite using a substantially larger architecture.

  • S1: FALA-G outperforms ACT-ViT across all seeds. Moreover, ACT-ViT generalizes less effectively than the standard linear probe for harder folds (MNLI).
  • S2: FALA-G achieves stronger performance in interval coverage. ACT-ViT struggles to produce input-dependent prediction intervals, resulting in coverage comparable to the linear probe (0.049 versus 0.020), both substantially below FALA-G (0.468).
  • S3: FALA-G achieves a higher average score than ACT-ViT, although the difference is not statistically significant given the observed seed variability.

Importantly, ACT-ViT processes the entire layer × token activation tensor and has 2.9 times as many parameters as FALA-G. Nevertheless, it does not outperform FALA-G on any signal and often performs substantially worse. These findings provide additional evidence that the benefits of FALA-G do not simply arise from accessing more activations or increasing model capacity, but from how the activation information is aggregated and selectively used across layers.

We have incorporated ACT-ViT into Figure 1 in the main text and Tables 12-14 in Appendix G.

W2 (and Q2). Single-seed results and absence of matched multi-seed evaluation

We agree that evaluating training variability is important, particularly when performance differences between methods are small. To address this concern, we reran methods on all three signals using two additional random seeds, while keeping the evaluation folds and hyperparameters fixed. The results are reported in Tables 15-17 of Appendix H.

The multi-seed results support our original conclusions for S1 and S2. For S3, however, we observe substantial variability that prevents us from establishing a statistically significant advantage for FALA-G over the baselines. For instance, per-fold standard deviations reach 0.14 for FALA-G on StackEdu and 0.12 for ACT-ViT on arXiv, whereas the differences between method means in Table 16 are at most 0.02.

We have therefore revised our claims regarding S3 and no longer assert a clear ranking between methods on this signal. The revised manuscript also includes the complete multi-seed results in Appendix H (Tables 15-17).

We thank the reviewer for these suggestions, which have led to a more comprehensive experimental comparison and a better characterization of the robustness of our findings.

I want to thank the authors for their responses and added experiments. The revisions made satisfy the methodological concerns that I’ve raised, particularly regarding the comparison against ACT-ViT and the variability across training runs, and as such I’ll be increasing my set Soundness score from 2->3. I’ll be maintaining the original overall rating of 3.

Dear Reviewer HbRz,

Thank you for the follow-up and for raising the Soundness score. We are glad the added ACT-ViT comparison and run-to-run variability analysis addressed your concerns.

Comments on the paper

1 comment

General response to all reviewers

(We refer to reviewers in the order their reviews were posted: R1 = HbRz, R2 = oQue, R3 = U6VN.)

We thank all reviewers for their feedback. Several reviewers raised overlapping concerns, most notably the lack of a comparison to ACT-ViT and the lack of multi-seed evaluation. We address these common points below. Points raised by individual reviewers are addressed in our replies to each of them. Both are supported by additional experiments and a revised PDF; changes are marked in blue, and table and section numbers below refer to the revised PDF.

We also want to highlight two aspects of the paper beyond the architecture comparison.

In response to R2's question about why we fix the Gumbel selector size at K=3 (the number of layers each architecture selects) rather than tuning it per signal, our selection hyperparameters were tuned once, on a single fold of one signal, and then reused as-is across every other fold, signal, and host architecture. This is a deliberate choice, not an oversight: further tuning would likely raise the reported numbers, but at our label budgets it would also risk reporting performance inflated by fitting to validation signal rather than genuine generalization. We would rather report a number we trust than a higher one we don't.

Separately, across nine distributionally robust training objectives (two newly added, IRM and IRM-Games) and two host architectures, none reliably outperforms ERM. We think this negative result is as important a contribution of the paper as the architecture comparison itself, and we have added further evidence for it in this revision.

Main changes

Raised byChangeLocation in revised PDF
R1-W1, R2-W1ACT-ViT baseline addedFigure 1; Tables 12–14 (Appendix G)
R1-W2, R2-W2Matched multi-seed evaluation for all three signalsAppendix H, Tables 15–17
R2, R3S1 and S3 claims narrowed to what the multi-seed results supportThroughout; Appendix H
R2, R3Random-init control on S3 reframed as a surface-form reference, not a bar an architecture must clear; row relabeled accordinglySection 4.2; Appendix G
R3Selector ablation: fixed layer window and noise-free selector, compared with the learned Gumbel selectorAppendix L
R2Discussion added on the relationship to neural functionals (Zhou et al., NeurIPS 2023) and graph neural networks over neural networks (Kofinas et al., ICLR 2024)Section 6
R2Clarified that hyperparameters (Gumbel-Softmax K=3) were tuned once on S1 and reused across signals/hosts by design, not as a shortcutSection 3.1.3
Authors' initiativeTwo further distributionally robust objectives (IRM, IRM-Games) added; none of nine objectives reliably outperforms ERM on either host architectureFigure 2 (main text); per-fold results in Table 11
Authors' initiativet-SNE projection of checkpoint features, visualizing the architecture-vs-objective contrastAppendix K
Authors' initiativeFinal-state invariance diagnostic by fold and objective, reported separately for FALA-G and WAP-GAppendix I.2, Figures 7–8

We hope these additions address the shared concerns raised across reviews. We welcome further discussion during the remainder of the discussion period.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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