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Under review as a conference paper at ICLR 2027

Rethinking Neural Thickets Without Weight Perturbations

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Abstract

The Neural Thickets hypothesis posits that pretrained language models lie in dense neighborhoods of task-specific experts in weight space, which random Gaussian perturbations can uncover. We reproduce the reported gains, but show that they do not require this geometric explanation. Perturbing a single decoder block already recovers much of the improvement, while keeping the model entirely frozen and adding a random bias to its output logits matches or exceeds full-weight perturbations on most reasoning tasks. This suggests an alternative explanation based on output diversity, validation-based selection, and voting. We formalize this view as Perturb-Select-Vote (PSV), a general procedure that generates perturbed predictors, selects high-performing members on a small validation set, and aggregates their predictions. This interpretation connects Neural Thickets to established inference-time methods, including sampling, self-consistency, and verifier-guided selection. A first-order analysis further shows that small weight perturbations act primarily through their induced logit shifts. We extend this analysis to vision, where logit PSV substantially improves performance under domain shift, including on Earth observation, while full-weight perturbations provide little additional benefit. Together, these results suggest that the gains attributed to nearby weight-space experts can instead be obtained through output diversity, selection, and voting. Logit PSV realizes these benefits with a fully frozen model, providing a simple, training-free alternative to full-weight perturbation ensembles across language and vision.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Neural Thickets, weight perturbation, logit perturbation, ensembles, self-consistency, training-free adaptation, domain shift

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_RyNzOpenReview ↗
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3(+1)
Confidence
2
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Paper summary

The paper revisits the Neural Thickets hypothesis, which proposes that pretrained LLMs are surrounded by dense neighborhoods of task-specific experts in weight space that can be discovered through random Gaussian weight perturbations. The authors challenge whether weight perturbations are actually necessary to obtain these performance improvements. They first demonstrate that perturbing only a single decoder block recovers much of the accuracy improvement achieved through full-weight perturbations. They then show that applying PSV directly to the output logits of a fully frozen model matches or even exceeds full-weight perturbation ensembles on most evaluated reasoning tasks. Finally, they extend their investigation to vision models, where output-logit perturbations similarly outperform weight perturbations under domain shift.

Critical strengths
  1. The paper investigates an interesting and important question concerning the Neural Thickets Hypothesis, namely, whether the improvements actually require full weight space perturbations. For this, the authors propose a simple yet elegant alternative that achieves competitive performance without modifying the weights.

  2. I appreciate that the authors extend their experiments beyond language models to vision classification under domain shift, broadening the scope of the analysis.

Critical weaknesses
  1. The absence of uncertainty estimates for the main experimental results. Both full-weight and logit PSV are inherently stochastic. The central results in Figures 2-4 and Tables 1, 3, and 5 are reported without standard deviations or confidence intervals across independent runs. This is particularly concerning as several reported differences are relatively small.

  2. The paper demonstrates strong ensemble performance, it remains unclear how well individual selected logit PSV members generalize to held-out examples. Although the ensemble-size sweeps include the single-member case, I would appreciate a more systematic analysis of the test accuracy distributions of individual randomly sampled and selected members.

  3. The authors themselves acknowledge that larger models may exhibit weight-space effects that output-logit perturbations cannot capture. Evaluating at least one substantially larger model would provide valuable evidence about whether the proposed explanation continues to hold at larger scales.

Questions for authors
  1. Can you provide standard deviations and/or confidence intervals across independent runs with different random seeds, for all the main experimental results?

  2. Can you provide the systematic analysis of the test accuracy distributions of individual randomly sampled and selected members of the logit PSV methodology?

  3. How large are the differences between the original full weight perturbation neural thicket methodology and your logit PSV methodology on a substantially larger model, please include standard deviations?

5 comments

Q1. "Can you provide standard deviations and/or confidence intervals across independent runs with different random seeds, for all the main experimental results?"

We thank the reveiwer for the suggestion. Every table and figure is now repeated with three seeds of the perturbations (and of TT-MV's sampling) on the same selection and test items. The paper now reports mean ± s.d. and paired 95% CIs; Figures 2–4 show error bars (App. D.2). Spread across seeds:

results.d. across seeds (accuracy points)
Matched comparison, 35 cells (Table 6)0.0–2.2 (median 0.45)
Per-block profile (Fig. 2)0.1–1.1
KK-curves (Figs. 6–8)median 0.6–0.7, larger at K≤2K\le2

Replicates that also redraw the selection set give the same picture (Table 10).

Q2. "Can you provide the systematic analysis of the test accuracy distributions of individual randomly sampled and selected members of the logit PSV methodology?"

Yes, for both families: Tables 11–12 (App. E) cover every model and task. Logit PSV examples (N=5000N{=}5000, test accuracy):

cellbase50 selected members (mean ± s.d.)50 random membersvote of the selected
OLMo-7B MATH-50051.055.9 ± 2.643.4 ± 7.972.7
Qwen-1.5B GSM8K60.464.8 ± 1.659.3 ± 4.780.0
Qwen-3B Countdown13.716.2 ± 2.711.7 ± 3.357.1
Llama-8B Countdown9.518.4 ± 2.79.3 ± 3.965.6

Selected members are only slightly better than the base model on held-out data; across all cells, the median is +0.1 points. Random members are at or below the base. Most of the gain comes from the vote.

We also ran this analysis for vision: FMoW, DINOv3 S–7B, 10 pools of 3500 members each.

Random memberSelected member (top 10)
Mean test Δ, worst-region accuracy−10 to −11+2.7 to +3.7
Members that beat the base model13–18%98–100%
Validation Δ → test Δ–+2.6..+4.2 → +2.7..+3.7

A random bias usually hurts, but selection reliably finds members that help. Their validation gain carries over almost unchanged to held-out test examples. Averaging the 10 selected biases then adds about one more point (+4.1 to +4.7).

Q3. "How large are the differences between the original full weight perturbation neural thicket methodology and your logit PSV methodology on a substantially larger model, please include standard deviations?"

Qwen2.5-32B-Instruct, three seeds, fixed selection and test sets (App. C.3; also our reply to E6hK):

Qwen2.5-32B (3 seeds)TT-MVfull-weight PSVlogit PSVlogit − full-weight [95% CI]
Countdown67.2 ± 0.269.4 ± 0.170.5 ± 0.2+1.1 [+0.5, +1.6]
GSM8K92.6 ± 0.392.6 ± 0.093.2 ± 0.1+0.6 [+0.2, +1.0]
MATH-50078.4 ± 0.480.7 ± 0.377.6 ± 0.7−3.1 [−5.1, −1.3]
OlympiadBench54.8 ± 0.356.9 ± 1.254.1 ± 0.1−2.8 [−4.3, −1.4]

Logit PSV matches or beats full-weight PSV on Countdown and GSM8K, and trails it by about 3 points on hard math. There, an LM-head-only perturbation recovers about 60% of the difference. We report this as a limitation.

In vision, DINOv3-7B (6.7B parameters) is the largest model of its family. Across the family, from 21M to 6.7B parameters, the logit-PSV gain stays flat (+4.1 to +4.7), and weight perturbations stay near zero even at the largest size (Table 3). We see no sign of a weight-space effect emerging with scale in vision.

Thank you for the detailed rebuttal and additional experiments. The new results address my main concerns, which inclines me to increase my score.

However, I cannot find the revised manuscript containing the referenced experiments and tables. Could the authors clarify where the updated PDF is?

AuthorsOpenReview ↗

Revised version now avilable

Dear Reviewer,

Thank you for your feedback. It appears that the revised manuscript was not uploaded correctly. This should now be fixed, and the updated PDF should be available.

Please do not hesitate to reach out if you have any further questions or need additional clarification.

Reviewer_E6hKOpenReview ↗
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Paper summary

This paper challenges the "Neural Thickets" hypothesis, which claims LLMs have dense neighborhoods of task experts in weight space discoverable via random perturbation. The authors show the same gains arise from perturbing just a single decoder block, or even just adding a random bias to the output logits of a fully frozen model. They formalize this as "Perturb-Select-Vote" (PSV), link it to self-consistency and best-of-N, and extend the finding to vision domain.

Critical strengths
  • Systematic ablation ladder (full-weight → single decoder block → single component → logits only) isolates exactly which part of the mechanism drives the gain, rather than just reporting an alternative that also works.
  • Strong, consistent results across 4 model scales and 7 tasks; logit-only version matches/beats full-weight perturbation.
  • Vision extension adds an independent modality supporting the same conclusion.
Critical weaknesses
  • Stops at 7B; the original hypothesis predicts effects grow with scale, so the largest-scale regime is untested.
  • Vision evidence is much thinner than language evidence (2 datasets, 1 backbone, K=10) despite similarly strong conclusions drawn.
  • The vision extension has no comparison to a fine-tuning or domain-adaptation training baseline — unlike language, where Gan & Isola (2026) already established competitiveness with PPO/GRPO, vision gains are only benchmarked against closed-form recalibration, leaving it unclear whether logit PSV is practically competitive there. The paper also doesn't test vision-language models, which would be a natural bridge between the two settings studied separately.
Questions for authors

Please refer to Weaknesses Section

2 comments
AuthorsOpenReview ↗

Answer 1/2

W1. "Stops at 7B; the original hypothesis predicts effects grow with scale, so the largest-scale regime is untested."

We add Qwen2.5-32B-Instruct, the same family as our 0.5–3B models, on four tasks. Each cell has three seeds on fixed selection and test sets (App. C.3, Tables 7–8):

Qwen2.5-32B (3 seeds)TT-MVfull-weight PSVlogit PSVlogit − full-weight [95% CI]
Countdown67.2 ± 0.269.4 ± 0.170.5 ± 0.2+1.1 [+0.5, +1.6]
GSM8K92.6 ± 0.392.6 ± 0.093.2 ± 0.1+0.6 [+0.2, +1.0]
MATH-50078.4 ± 0.480.7 ± 0.377.6 ± 0.7−3.1 [−5.1, −1.3]
OlympiadBench54.8 ± 0.356.9 ± 1.254.1 ± 0.1−2.8 [−4.3, −1.4]
  • Countdown and GSM8K. Logit PSV matches or beats full-weight PSV and TT-MV.
  • MATH-500 and OlympiadBench. Full-weight PSV leads by about 3 points. This lead does not appear to come from selection: 50 random full-weight members reach 80.6 on MATH-500, vs 81.4 for the selected ones. Perturbing the LM head alone reaches 79.4, about 60% of the way from logit to full-weight PSV, while the last decoder block alone (77.8) does not.

At this scale on hard math, the useful variation appears to depend on the input, which a constant bias cannot capture. It is largely available at the output layer, without a search for rare experts. We report this as a limitation (Sec. 6).

W2. "Vision evidence is much thinner than language evidence (2 datasets, 1 backbone, K=10) despite similarly strong conclusions drawn."

We agree that the vision experiments are less fleshed out than the LLM section,a nd thank the reviewers for their pointers on how to remedy this issue. We added six additional backbones under one consistent protocol: the DINOv3 family from S to 7B, a supervised DeiT-III, and I-JEPA. Error bars come from 10 independent bias pools.

As a control, we repeat the procedure on FMoW's in-distribution split. Its validation and test images come from the same years as the training data. The bias is selected on in-distribution validation and reported on in-distribution test.

BackboneBase (OOD)Logit-PSV Δ (OOD)Logit-PSV Δ (in-distribution control)
DINOv3-S32.3+4.1±0.7−0.4
DINOv3-B34.8+4.7±0.4−0.3
DINOv3-L35.4+4.7±0.5−0.3
DINOv3-H+39.1+4.2±0.4−0.1
DINOv3-7B40.1+4.2±0.3+0.2
DeiT-III-L (supervised)32.2+2.1±0.70.0
I-JEPA-H26.3+3.7±0.5+0.1

The gain holds across scale and training paradigm, and it disappears without distribution shift. That is the pattern our recalibration account predicts.

On K: the vision pool is N = 3500 biases, the same order as the language setting (N = 1000–5000). So K = 10 is not a budget choice:

  • When K is chosen on validation, it comes out small (5 to 20).
  • Larger K lowers the gain. For 7B we get +6.4, +3.7 and +1.0 at K = 10, 50 and 500, and about 0 at K = N.
  • The reason is selection. Keeping more members means keeping worse ones, which averages the useful tilt away. In a single-step classifier only a few logit directions matter, so beyond about K = 5 there is little noise left to average out.

We will add this analysis to the appendix. We will also tone down the vision conclusions, stating them as specific to classification under distribution shift.

AuthorsOpenReview ↗

Answer 2/2

W3. "The vision extension has no comparison to a fine-tuning or domain-adaptation training baseline — unlike language, where Gan & Isola (2026) already established competitiveness with PPO/GRPO, vision gains are only benchmarked against closed-form recalibration, leaving it unclear whether logit PSV is practically competitive there. "

We compare logit PSV, used as a test-time adaptation method, against adaptation baselines. We follow the protocol of FINO (NeurIPS 2026): DINOv3 ViT-L on FMoW-WILDS, a 40-epoch attentive probe, worst-group accuracy. The attentive probe is why the frozen base (45.8) is higher than the linear-probe numbers above. Baseline numbers are as reported by FINO under the same protocol.

MethodLabels used for adaptationWorst-group acc.
Frozen backbone–45.8±1.1
Frozen + logit PSVvalidation only, no training47.9±1.0
Supervised fine-tuningtraining labels40.5
GroupDROtraining labels and groups46.4
Self-supervised adaptationnone48.4
FINOmetadata53.3±0.8
  • Logit PSV beats supervised fine-tuning and GroupDRO, and comes close to self-supervised adaptation.
  • It needs no backbone training: minutes on a CPU, versus tens to hundreds of GPU-hours.
  • It stays well below representation adaptation such as FINO, which is what one expects from a pure output recalibration.

So logit PSV is a practical, cheap test-time correction when a small labelled validation set from the target domain is available. It does not replace adapting the representation.

W3 "The paper also doesn't test vision-language models, which would be a natural bridge between the two settings studied separately."

We agree that extending the analysis to vision-language models would provide a natural bridge between our language and vision experiments. However, VLMs introduce additional design choices and interactions that are absent from either setting alone, including the choice of representation to perturb, cross-modal fusion, and the respective roles of the vision encoder and language model. We therefore believe that a meaningful study would require a dedicated analysis beyond the scope of the present paper. Given the already broad scope of the current work, we reserve this direction as promising future work.

Reviewer_jZv4OpenReview ↗
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3
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Paper summary

The paper revisits the Neural Thickets hypothesis by asking whether the gains from ensembles of randomly perturbed models require changes to pretrained weights. It frames the underlying procedure as Perturb–Select–Vote (PSV), in which candidate predictors are generated through random perturbations, ranked on a labeled validation set, and combined through voting. Logit PSV keeps the pretrained model frozen and adds a randomly sampled vocabulary-level bias that remains fixed across decoding steps and inputs for each ensemble member. Experiments across several language-model sizes and reasoning benchmarks show that this output-only intervention often matches or exceeds full-weight perturbation ensembles, while additional ablations demonstrate that perturbing individual decoder blocks or components can recover substantial gains. The theoretical analysis characterizes voting and selection, distinguishes persistent perturbations from ordinary temperature sampling, and examines how small weight perturbations induce changes in output logits. Experiments with pretrained vision models further suggest that output recalibration can account for substantial improvements under distribution shift.

Critical strengths
  1. The paper shows that persistent random logit biases applied to a frozen model can recover much of the benefit of full-weight perturbation ensembles. In Table 5, logit PSV matches or exceeds full-weight PSV in 21 of the 26 reported task–model settings, spanning multiple model sizes and task families (although I'm always suspicious of Qwen2.5 results!). This is consequential because it demonstrates that modifying pretrained weights is unnecessary for achieving many of the reported gains and provides a straightforward alternative that avoids managing perturbed parameter configurations.

  2. The paper examines localized weight perturbations, temperature-tuned majority voting, and deterministic output recalibration in vision. These comparisons show when simpler interventions can account for the observed improvements, while the negative results on balanced ImageNet and the limited gains from stacking perturbations help define the boundaries of the findings (thanks to the authors for providing negative results).

Critical weaknesses
  1. The experiments support the claim that output-only perturbations can achieve competitive accuracy, but they do not establish that weight and logit perturbations succeed through the same mechanism. The first-order expansion in Section 4.5,
\approx \ell_\theta(s)+\sigma J(s)\epsilon,$$ describes an input- and prefix-dependent shift, whereas logit PSV adds the same vocabulary bias at every state $s=(x,y_{<t})$. These are different families of predictors. Moreover, the reported 89.7% agreement concerns token changes along fixed, teacher-forced continuations; it does not establish agreement between complete generated answers or between weight perturbations and constant logit biases. I also think the attribution of weak-model gains to selection is confounded. Comparing temperature-tuned majority voting with logit PSV simultaneously changes the perturbation distribution, persistence across decoding steps, and validation-based selection. The paper’s own persistent-noise example shows that persistence alone can change the answer distribution substantially. A decisive control would compare selected and randomly chosen members from the **same persistent Gaussian population**, with identical noise scale and ensemble size. These limitations matter because explaining the source of the gains is a central contribution, beyond demonstrating competitive performance. --- 2) The principal accuracy comparisons lack clearly reported variability across candidate populations, selection sets, and repeated runs. This is consequential when selecting from thousands of candidates using only 200 examples, particularly given the paper’s observation that the best individual member improves selection accuracy by 11 points but held-out accuracy by only 2.4 points (Appendix C, p. 22). The reported advantages also depend substantially on the comparison budget. On OLMo MATH-500, logit PSV reaches 81.7%, compared with 74.7% for full-weight PSV at $N=1000$ in Table 5, but 80.7% at $N=5000$ in Table 1. Thus, the apparent advantage changes from 7.0 points to 1.0 point. These can be legitimate budget-dependent results, but the narrative needs a clear mapping between each comparison and its population size, tuning budget, and selected hyperparameters. Without paired uncertainty, the smaller differences cannot establish superiority. Also, this paper leaves important implementation choices unspecified, including complete noise and temperature grids, tuning splits, dataset-specific answer equivalence and voting rules, and several vision-training settings. A run-level specification, executable configurations, and uncertainty across the full selection procedure are needed to assess robustness and reproduce the central findings. I know this is appendix material; however, we need it in 2026! --- 3) Appendix C reports a cosine standard deviation of $4.5\times10^{-3}$ between random perturbation directions. Under the isotropic Gaussian perturbation model in Equation 3, independent normalized directions in $d$ dimensions satisfy $$\operatorname{Var}\left(\frac{\epsilon_1^\top\epsilon_2} {\|\epsilon_1\|\|\epsilon_2\|}\right)=\frac{1}{d}.$$ For approximately seven billion parameters, the expected standard deviation is therefore about $1.2\times10^{-5}$, roughly 376 times smaller than the reported value. A projection, coordinate subsample, layerwise calculation, or different perturbation distribution could explain this discrepancy, but none is specified. The exact vectors and calculation must be clarified before the statistic can support conclusions about the full weight space (I double-checked this observation with AI, without submitting your paper to AI; I just verified it). The interpretation of the remaining diagnostics is also too strong. Near-orthogonality is expected in high dimensions and does not exclude a dense population of useful models. Likewise, averaging perturbations reduces their effective scale, so the collapse of an unrescaled weight soup is not a clean test of connectivity. That being said, I think the geometric conclusions require explicit scale controls and a precisely defined interpolation path. --- 4. Equation 9 defines a class bias using true and predicted frequencies on the “validation group of interest,” but does not clearly specify whether these frequencies are pooled or group-specific, whether predictions are hard labels or probabilities, how zero frequencies are handled, or whether group information is required at test time. These choices directly affect the interpretation and reproducibility of the worst-group results. The formula $$b_c=\log\pi_{\mathrm{true}}(c)-\log\pi_{\mathrm{pred}}(c)$$ also does not generally guarantee marginal matching or improved accuracy; predicted class frequencies are not automatically the source priors required by a standard label-shift correction. For binary Waterbirds classification, each fixed-bias member is simply a threshold on the frozen model’s logit difference. Voting over these members reduces to another threshold rule, subject to the specified tie-breaking convention. A **single threshold directly optimized for the same validation objective** is therefore an essential baseline. Without this comparison and a precise group-handling protocol, it remains unclear what the randomized ensemble contributes beyond ordinary decision-threshold adjustment.
Questions for authors
  1. Can you isolate the contribution of validation-based selection? Please compare the top-KK selected members with KK uniformly chosen members from the same persistent Gaussian population, holding the noise scale, ensemble size, and decoding settings fixed. How much of the improvement remains without selection, particularly in the weak-model settings where TT-MV performs poorly? This comparison would help distinguish selection effects from differences in perturbation distribution and persistence.

  2. What evidence supports a shared mechanism between weight perturbations and fixed logit biases? The linearized shift σJ(s)ϵ\sigma J(s)\epsilon depends on the input and prefix, whereas logit PSV uses a state-independent bias. Can you clarify how the first-order analysis supports the proposed connection beyond showing that weight perturbations change output logits? For the linearization experiment, can you also report false-positive token changes and agreement on final answers under free-running generation, in addition to agreement on perturbation-induced changes at teacher-forced prefixes?

  3. Can you provide a unified specification and uncertainty analysis for the main comparisons? Please identify the population size NN, ensemble size KK, noise scale σ\sigma, temperature TT, tuning budget, and tuning split associated with each main result. In particular, how should readers compare the MATH-500 results of 74.7% for full-weight PSV in Table 5, 80.7% in Table 1, and 81.7% for logit PSV? How stable are these differences across independently sampled candidate populations and selection sets, and can you provide paired confidence intervals?

  4. How were the reported perturbation-direction cosines computed? Appendix C reports a random-pair cosine standard deviation of 4.5×10−34.5\times10^{-3}, whereas independent isotropic Gaussian directions in approximately seven billion dimensions would have standard deviation 1/d≈1.2×10−51/\sqrt{d}\approx1.2\times10^{-5}. Were the vectors projected, subsampled, normalized by layer, or otherwise transformed? Please specify the calculation and clarify whether the soup and midpoint conclusions persist after controlling for changes in perturbation norm.

  5. Can you specify the vision recalibration protocol and compare it with direct threshold tuning? In Equation 9, what precisely is the “validation group of interest,” are predicted frequencies computed from hard labels or soft probabilities, and how are zero frequencies handled? Are biases global or group-specific, and is group information needed at test time? For Waterbirds, how does logit PSV compare with a single decision threshold optimized directly for the same validation objective, given that voting over fixed-bias binary classifiers reduces to a threshold rule under a fixed tie convention?

5 comments
AuthorsOpenReview ↗

Answer 1/3

" [evaluate other big models beyond] Qwen2.5"

We added additional models to complement our evaluation. The matched comparison (Table 6) now also covers OLMo-3-7B and Llama-3.1-8B-Instruct, the model with the original study's largest gain. On Llama, logit − full-weight at K=50K{=}50 (mean over three seeds + [95% confidence interval]):

CountdownGSM8KMATH-500OlympiadBenchMBPPROCStoriesUSPTO
+2.5 [+1.7, +3.4]−0.8 [−1.6, +0.0]−1.0 [−4.6, +2.3]+0.1 [−1.8, +2.1]−1.8 [−4.1, +0.4]−5.7 [−6.0, −5.4]−7.5 [−9.3, −5.7]

The reasoning tasks are tied or favor logit PSV, and the two label-prediction tasks favor full-weight PSV. This is the same pattern as on OLMo and the larger Qwen models.

Q1. "Can you isolate the contribution of validation-based selection? Please compare the top-KK selected members with KK uniformly chosen members from the same persistent Gaussian population, holding the noise scale, ensemble size, and decoding settings fixed. How much of the improvement remains without selection, particularly in the weak-model settings where TT-MV performs poorly?"

We ran this control for every model, task and family: KK members drawn uniformly from the same persistent population, with the same noise-scale mix, KK and decoding (App. E). Examples at K=50K{=}50 (full-weight family):

cellbase50 random members50 selected members
OLMo-7B Countdown66.690.7 ± 0.391.8
OLMo-7B MATH-50051.066.5 ± 0.970.0
Qwen-1.5B Countdown (weak base)12.520.1 ± 2.833.2
Llama-8B Countdown (weak base)9.554.7 ± 1.462.4
Llama-8B ROCStories51.851.0 ± 0.660.7
  • Without selection. Over the 45 reasoning and code cells with a gain, the vote without selection achieves a median 93% of the gain (IQR 85–101%). Selection adds a median of +0.7 points (Table 11).
  • With selection. Selection matters mainly when most members are poor: USPTO, ROCStories with Llama, and weak-model Countdown, i.e. where TT-MV struggles. There it relies on the labels. Ranking the same members by answer format or by agreement with the majority does not recover the gain; on Qwen-1.5B Countdown, format-based selection reaches 2.6 vs 20.4 for random members (Table 13).
  • Noise type vs. persistence (21 cells, median change, Table 14). TT-MV → logit noise redrawn at every step: +0.3. Per-step noise → persistent random members: −0.2. Random → selected members: +1.3. Persistence seems to matter because it makes members selectable, not by itself.

Q2. "What evidence supports a shared mechanism between weight perturbations and fixed logit biases? The linearized shift σJ(s)ϵ\sigma J(s)\epsilon depends on the input and prefix, whereas logit PSV uses a state-independent bias. Can you clarify how the first-order analysis supports the proposed connection beyond showing that weight perturbations change output logits? For the linearization experiment, can you also report false-positive token changes and agreement on final answers under free-running generation, in addition to agreement on perturbation-induced changes at teacher-forced prefixes?"

We agree that the weight perturbations and logit perturbations are not necessarily equivalent. Our proposed shared mechanism is output diversity, selection, and voting. We understand though why some phrasing might invite the reader to assume equivalence between them. Our main finding is that constant logit biases are quite competitive without modifying the weights. This doesn’t need the two methods to produce identical predictions, or a weight perturbation’s induced logit shift to be constant. We have clarified this in Section 4.5 and will narrow the role of the first-order analysis. We also ran the suggested experiments following the setup in Section 4.5, where we compare each weight-perturbed model with its first-order approximation using OLMo-3-7B-Instruct on Countdown. Values in the table below are means ± 95% CIs over perturbations. The linearization doesn’t hold as well with free-running generation, which is expected given compounding errors. We’ve added this to Appendix B.5 and restricted the scope to local token effects. Still, the ensemble comparisons and selection controls support the broader diversity–selection–voting account.

AuthorsOpenReview ↗

Answer 2/3

Q2 (part 1/2)

DiagnosticResult
Agreement on token changes at teacher-forced prefixes89.7 ± 2.0%
False-positive token changes at teacher-forced prefixes0.6 ± 0.2%
Agreement on final answers under free-running generation85.5 ± 1.3%
Agreement restricted to cases where the answer changes56.6 ± 5.9%

The first-order analysis also helps explain the smaller query/key perturbation gains in Fig. 3. Appendix B.5 applies the same linearization to individual components, and shows how the attention softmax can attenuate query/key perturbations before they reach the logits. This is consistent with the query/key path recovering 85–89% of the full-weight gain, compared with 96–103% for the other components (lines 1094–1095). The teacher-forced experiment is meant as a sanity check that the first-order approximation captures actual token changes at our noise scale, which supports the analysis in Appendix B.5.

Q3. "Can you provide a unified specification and uncertainty analysis for the main comparisons? Please identify the population size NN, ensemble size KK, noise scale σ\sigma, temperature TT, tuning budget, and tuning split associated with each main result. In particular, how should readers compare the MATH-500 results of 74.7% for full-weight PSV in Table 5, 80.7% in Table 1, and 81.7% for logit PSV? How stable are these differences across independently sampled candidate populations and selection sets, and can you provide paired confidence intervals?"

Specification. Table 9 (App. D.1) lists NN, KK, σ\sigma, TT, selection split and tuning for every result, with the voting and answer-equivalence rules. The code will be released upon acceptance.

The three MATH-500 numbers come from different configurations:

numberfamilyNNσ\sigma
74.7full-weight100010−310^{-3}
80.7full-weight5000grid 1,2,3×10−31,2,3\times10^{-3}
81.7logit10002

The difference between 74.7 and 80.7 comes mostly from the noise scale available to selection, not from NN. 98 of the 128 top-ranked members of the N=5000N{=}5000 run use σ=3×10−3\sigma{=}3\times10^{-3}, and the vote saturates at a few hundred members. The like-for-like comparison is Table 6, with equal budgets and a grid per family. There, on OLMo MATH-500, logit PSV is ahead by +3.8 points [+1.7, +6.2] over three seeds.

Stability. Every comparison is repeated over three seeds with paired CIs. Replicates that also redraw the 200-item selection set (27 cells, 7 estimates each) give the same picture (App. D.2, Table 10).

Comment 3/3

Q4. "How were the reported perturbation-direction cosines computed? Appendix C reports a random-pair cosine standard deviation of 4.5×10−34.5\times10^{-3}, whereas independent isotropic Gaussian directions in approximately seven billion dimensions would have standard deviation 1/d≈1.2×10−51/\sqrt{d}\approx1.2\times10^{-5}. Were the vectors projected, subsampled, normalized by layer, or otherwise transformed? Please specify the calculation and clarify whether the soup and midpoint conclusions persist after controlling for changes in perturbation norm."

Thank you for checking this. The reported value came from a coordinate-subsampled estimator. Exact cosines over all 7.3×1097.3\times10^9 coordinates (App. G, Table 17):

noise recipeselected pairsrandom pairspredicted s.d.
per-tensor re-seeding (RandOpt code)(+0.2±11.1)×10−5(+0.2 \pm 11.1)\times10^{-5}(−0.1±10.8)×10−5(-0.1 \pm 10.8)\times10^{-5}10.8×10−510.8\times10^{-5}
i.i.d. per tensor(+0.05±1.16)×10−5(+0.05 \pm 1.16)\times10^{-5}(+0.01±1.15)×10−5(+0.01 \pm 1.15)\times10^{-5}1/d=1.17×10−51/\sqrt{d}=1.17\times10^{-5}

The spread exceeds 1/d1/\sqrt{d} because RandOpt's released code re-seeds every tensor with the member's seed, so same-shaped tensors share their noise. With i.i.d. noise, PSV accuracy is unchanged (90.5 / 89.5 / 69.3 vs 91.3 / 89.4 / 68.6 on Countdown / GSM8K / MATH-500). Selected and random directions are indistinguishable. As you note, this says nothing about density, and we do not use make any claim in that regard.

The midpoint is norm-preserving and shows no barrier for selected or random pairs. With norm control, the soup tells a more nuanced story (OLMo-7B, K=50K{=}50, Table 18):

taskbasesoup (unrescaled)soup ×√K, selectedsoup ×√K, randomvote
Countdown66.667.369.666.691.8
GSM8K87.587.688.786.089.6
MATH-50051.052.761.044.070.0

The selected perturbations share a useful direction, which recovers roughly 10–50% of the voting gain, but voting provides most of it.

AuthorsOpenReview ↗

Answer 3/3

Q5. "Can you specify the vision recalibration protocol and compare it with direct threshold tuning?

We thank the reviewer for the careful reading. We answer their questions below.

"Equation 9 [...] does not clearly specify whether these frequencies are pooled or group-specific, whether predictions are hard labels or probabilities, how zero frequencies are handled, or whether group information is required at test time."

This is correct, and we will add the full protocol to the appendix:

  • Group of interest. The region on which the base probe has the lowest validation accuracy (Africa for every backbone).
  • Frequencies are per group, not pooled. π_true(c) is the fraction of that region's validation images with label c. π_pred(c) is the fraction of them the model predicts as c.
  • Predictions and zero counts. We use hard (argmax) predictions. With 62 classes, some classes are never predicted in a region, so we use add-one (Laplace) smoothing to avoid log 0. Soft probabilities (the average softmax) need no smoothing, since probabilities are never exactly zero. They give similar results: +3.9 to +5.5 across DINOv3 sizes, versus +3.8 to +5.3 with hard counts.
  • No group labels at test time. A single global bias is added to every test image. Group labels are used only on validation, to pick the region.

"The formula also does not generally guarantee marginal matching or improved accuracy; predicted class frequencies are not automatically the source priors required by a standard label-shift correction."

Correct as well, and this is intended. Eq. 9 does not estimate source priors. It recalibrates the model's own output prior: how often this particular probe predicts each class on the group of interest, pulled towards the true class frequencies. Our claim is that this recalibration is the mechanism behind logit PSV in vision.

The table below supports it. The closed form tracks logit PSV across model sizes. A standard label-shift correction, which adds log π_val(y) − log π_train(y) built from the true label frequencies of the validation and training sets, recovers much less.

FMoW worst-region accuracy, test ΔSBLH+7B
Closed form (Eq. 9)+5.3+4.8+4.7+4.4+3.8
Logit PSV (K=10)+4.1+4.7+4.7+4.2+4.2
Standard label-shift correction+2.6+0.4+0.2−0.7+1.9

As the reviewer notes, none of these comes with a guarantee; the support is empirical. We will rephrase the text accordingly.

"For binary Waterbirds classification, each fixed-bias member is simply a threshold on the frozen model's logit difference. [...] A single threshold directly optimized for the same validation objective is therefore an essential baseline."

We agree. In the binary case each bias is a threshold, and a single threshold tuned on the same validation objective matches logit PSV, as we state in the paper (l. 447). This fits our main conclusion: in vision classification the gains come from recalibrating the output, and in the binary case recalibration is exactly a threshold.

"Can you isolate the contribution of validation-based selection? Please compare the top-K selected members with K uniformly chosen members from the same persistent Gaussian population, holding the noise scale, ensemble size [...] fixed."

For vision we ran exactly this control on FMoW (DINOv3 S–7B, same pool, same noise scales, K = 10):

  • Top-10 selected members: the ensemble gains +4.1 to +4.7.
  • 10 members chosen at random: the ensemble loses 3.4 to 7.1 points when their biases are averaged, and 1.0 to 1.7 points when they vote.

In vision, the whole gain comes from selection.

"[...] and several vision-training settings."

We will add them to the appendix:

  • Linear probe on frozen features. CLS plus average-pooled patch tokens. Images are resized to 448 and center-cropped to 336. We train with SGD (momentum 0.9, cosine schedule, no weight decay) at batch 512 for 6000 iterations (about 40 epochs). The learning rate is picked from 1e-4 to 5 on validation accuracy.
  • Logit PSV. N = 3500 random biases, within the N = 1000–5000 range of our language experiments. We keep the top K = 10 by validation worst-region accuracy and add the mean of the kept biases at test.

Table 3 correction. We also correct the FMoW row of Table 3. It now uses a better-tuned linear probe. The earlier probe had been trained with a smaller batch and a learning-rate grid that was too narrow, so it underfit. This does not change any of our conclusions or claims.

FMoW, DINOv3-7B, worst-region accuracyBaseLogit PSV (Δ)Closed form (Δ)
Before (submission)35.1+6.2+3.7
After (better-tuned probe)40.1+4.2±0.3+3.8

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response

We thank the reviewers for their careful reading and constructive suggestions. We ran the requested experiments and uploaded a revised PDF (changes in blue). The main points are summarized here, and each reply gives the key numbers with a pointer to the paper.

  • Uncertainty (jZv4, RyNz). Every table and figure is repeated with three seeds on fixed selection and test sets, and reports mean ± s.d. and paired 95% confidence intervals (CIs), see App. D. In the matched comparison (Table 6, N=5000N{=}5000 for both families, Llama-3.1-8B included), logit and full-weight PSV are statistically indistinguishable in 22 of 35 model–task cells. Logit PSV is ahead in 7, all reasoning tasks, and behind in 6, five of them label-prediction tasks.
  • Selection vs. voting (jZv4, RyNz). Voting over unselected members of the same population achieves a median 93% of the gain on reasoning and code tasks. Selection matters mainly where most members are poor, and there it relies on the labels (App. E).
  • Scale (E6hK, RyNz). On Qwen2.5-32B, logit PSV matches or beats full-weight PSV on Countdown and GSM8K and trails it by about 3 points on MATH-500 and OlympiadBench (App. C.3). We report this as a limitation.
  • Specification (jZv4). Table 9 gives every run's configuration and the voting rules (App. D.1). The code will be released upon acceptance.
  • Geometry (jZv4). Exact cosines, an i.i.d.-noise control and norm-controlled soups (App. G).
  • Mechanism (jZv4). We clarified that output diversity, selection, and voting explain the ensemble gains without requiring the weight and logit perturbations to produce identical predictions (Sec. 4.5, App. F.2). We also added the requested false-positive token-change and free-running answer-agreement diagnostics, and restrict the first-order claim to local token effects (App. B.5).
  • Vision (jZv4, E6hK). We substantially broadened the evaluation beyond the original setup. We tested seven backbones spanning 21M to 6.7B parameters, added uncertainty estimates over independent bias pools, and introduced an in-distribution control showing that the gain disappears without distribution shift. We also isolated the role of selection and compared logit PSV with standard adaptation baselines, confirming that its gains come from selecting useful output recalibrations rather than modifying the representation.

Dear Reviewers,

Thank you again for your valuable feedback. We have sought to address your concerns through additional experiments, clarifications, and revisions to the manuscript.

Please let us know if any points remain unclear or would benefit from further discussion. We would be happy to provide additional clarification.

Thank you for your time and consideration!

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

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