acceptodds
Withdrawn from ICLR 2027

Architectural Sampling: Test-Time Scaling via Computational Diversity in Frozen Vision-Language Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Test-time scaling often seeks better answers by sampling multiple responses from a frozen model, yet conventional temperature sampling generates every candidate along the same fixed computation path. We introduce architectural sampling, a training-free method that generates candidates through distinct forward computations by reusing selected blocks of decoder layers. Varying the block location and repetition count introduces computational diversity without updating model weights or adding auxiliary parameters. Across five Qwen checkpoints and twelve multimodal benchmarks, architectural sampling improves over standard-path temperature sampling by 6.58 percentage points on average at the same nine-candidate budget. Reusing early layers yields the strongest gains, and the improvement in candidate coverage persists even under greedy decoding. The resulting candidates show lower lexical overlap and improve accuracy when used as rollouts for label-free test-time reinforcement learning. These findings extend the benefits of our architectural sampling beyond candidate coverage, demonstrating more effective learning from a model's own outputs.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
VLMs, Test-time-adaptation

Reviews

Among:
Shape:
1234this paper, Bottom 25%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.75 over 4 reviews, above 25% of the others.
Reviewer_vPE4OpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes architectural sampling for frozen VLMs, generating candidate responses by varying the location and repetition count of reused decoder blocks. Experiments show improved candidate coverage over standard sampling and benefits when using these candidates for test-time learning.

Critical strengths

S1. The method is simple, requires no additional training for candidate generation, and introduces no new parameters.

S2. The evaluation spans multiple models and benchmarks, with generally consistent improvements. The ablations help characterize effective configurations.

Critical weaknesses

W1. The main concern is missing comparisons with closely related methods. Although the paper discusses Inner Loop Inference, Training-Free Looped Transformers, and CoLa, it compares experimentally primarily against standard decoding strategies. This limits the assessment of its contribution beyond existing layer-reuse techniques.

W2. The authors should provide additional experimental evidence to distinguish the benefit of architectural diversity from that of layer looping itself. The current comparison changes both whether layers are looped and whether candidates use different looping configurations. It therefore remains unclear whether the gains require complementary computation paths or can be explained by a stronger individual looping configuration.

The authors should also update the anonymous GitHub repository with the code for any additional experiments, which I intend to reproduce. I would be willing to raise my score if the authors adequately address these concerns.

Questions for authors

please see weakness.

5 comments

We thank the reviewer for their time and energy in reviewing our paper.

W1: Missing comparisons with Inner Loop Inference, Training-Free Looped Transformers, and CoLa

We disagree with this concern. It rests on a mischaracterization of both our contribution and the cited works. Status of the cited works. Inner Loop Inference is a five-page, non-peer-reviewed arXiv preprint. Training-Free Looped Transformers is under review at ICLR 2027, the same venue as our submission. We cited both for transparency. Citing a paper does not make it an established baseline.

CoLa is not comparable. There are four independent reasons:

  1. It studies text-only LLMs, not VLMs.

  2. Its per-input MCTS is guided by answer correctness. It is therefore an oracle analysis that requires ground-truth labels at test time, which makes it unusable in our label-free setting.

  3. It requires many forward passes per input. Our method needs a fixed set of nine configurations costing 10.5 decoder traversals.

  4. It searches for one best path per input and produces no candidate pool.

Comparing a label-free sampling method against a label-guided oracle search is not a meaningful experiment.

And most importantly None of these works is a sampling method. All three aim to improve a single forward pass. Our contribution is a candidate-generation technique that uses computation paths as a sampling axis. To our knowledge, no prior work does this. Benchmarking against single-path inference methods would misrepresent our contribution, and we will not add comparisons that mislead readers about what the method is for even if it means acceptance.

Out of respect for the reviewer, we report them in the new Table 4. We do not, however, recommend adding them to the paper as baselines. Doing so would mislead readers into believing these sampling methods existed before this work. They did not.

MethodCV-BenchMMStarAI2DA-OKVQAScienceQA
Standard decoding
Temperature88.4858.9384.8988.6588.75
Beam Search86.0952.6080.7887.1686.22
Top-k89.1260.2785.6589.6189.74
Top-p88.9159.8485.3789.2889.41
Architectural perturbations
Layer skipping [19]93.7862.2492.2093.9795.93
Layer dropout [10]88.8660.1287.6990.1390.48
Hidden-state noise89.8059.5888.1290.4892.12
Input-side test-time methods
Plan-and-Solve [37]85.3760.8783.8186.7288.05
Self-Refinement [23]76.3852.8077.4577.4783.19
Describe-then-Answer [28]83.9351.2777.8886.0380.61
Prompt Repetition [18]86.1654.4083.3487.8688.15
Architectural sampling96.4082.7393.4895.7297.97

Table 4: Comparison of candidate diversity sources on Qwen3-VL-8B under an equal nine-candidate budget (pass@9\mathrm{pass}@9). Best results are bolded.

W2: Separating architectural diversity from layer looping itself

We thank the reviewer for this constructive question. We have added a new analysis, “Do we need different architectural configurations?” (Section 5, Figure 5).

On MMStar, we drew all nine candidates from each single configuration and compared this with pooling one candidate per configuration, keeping the candidate budget and decoding temperature identical. Each configuration saturates quickly on its own, and the best one reaches only 67.53%. Pooling reaches 82.73%, which is 15.20 points higher, even though several of the pooled configurations are weak in isolation. The same holds on CV-Bench and MMMU (Supp. C). The gain therefore comes from diversity across computation paths, not from any individual looped path. This answers W2 directly and also settles W1.

Reviewer_i9PzOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes architectural sampling, a training-free method for generating candidate answers from a frozen VLM. A contiguous window of early decoder layers is applied repeatedly before the forward pass resumes, and each combination of window and repetition count yields one candidate. With one standard pass this gives nine candidates. Compared with nine temperature samples at the same temperature, pass@9 improves by 6.58 points on average across five Qwen checkpoints and twelve multimodal benchmarks. Ablations show that early windows work best, that pass@9 is unchanged under greedy decoding, and that the candidates have higher lexical diversity. Used as rollouts for TTRV, the candidates also improve pass@1.

Critical strengths

The paper raises a well-motivated question. Candidate-based test-time scaling depends on the diversity of the candidate pool, and existing decoding strategies introduce diversity only at the final sampling step while the computation before it is identical for every candidate. Moving the source of diversity into the computation path is a reasonable direction, and the proposed method is simple, requires no training or additional parameters, and applies to any open-weight model. The evaluation covers a reasonable number of checkpoints and benchmarks, and the appendix reports run-to-run variance and a cost analysis.

Critical weaknesses
  • W1. pass@9 on multiple-choice benchmarks cannot establish that the method is useful, and the baselines appear misconfigured. Most benchmarks have about four options, so a pool containing a few near-random but well-formed answers approaches the pass@9 ceiling regardless of whether those answers carry information. The gap between coverage and usable accuracy is well known [1], yet no majority-vote or other selection-based accuracy is reported. Two observations make this concern concrete. First, the temperature baselines are implausibly low: Qwen3-VL-8B reaches pass@9 of 48.56 on MMMU (Table 1), while the officially reported pass@1 of the Instruct model is about 69.6, and pass@9 cannot be below pass@1. Qwen3.5-VL-4B is 20 to 40 points below the 2B model of the same family on several benchmarks. This points to a prompt or answer-parsing issue, in which case part of the reported gain is recovery from a broken baseline. Second, prior work cited by the authors reports that naive layer repetition degrades outputs [2], so per-path quality is likely reduced. Per-path pass@1, majority-vote accuracy, and a check of the baselines against officially reported numbers are needed before the gains can be interpreted.
  • W2. Missing perturbation baselines. Table 4 only compares against output-side decoding strategies. The relevant baselines are perturbations of the computation itself, such as random layer skipping, hidden-state noise, inference-time dropout, or input augmentation [3]. Without these, it is unclear whether repeating layers specifically matters.
Questions for authors
  1. What is the pass@1 of each (window, r) configuration, and how does majority vote over the nine candidates compare with majority vote over nine temperature samples?
  2. Can the authors add equal-cost controls with random layer skipping, hidden-state noise, or inference-time dropout?
  3. Are errors across architectural candidates more independent than across temperature candidates?
  4. Why is the Qwen3.5-VL-4B baseline substantially below the 2B model?
2 comments

We thank the reviewer for their time and energy in reviewing our paper.

Coverage is the right metric. No selector, verifier, or learner can recover an answer that was never generated, so pass@k sets the ceiling for all of them. Coverage also drives RL. GRPO learns only when a rollout group contains both correct and incorrect answers. A group with uniform rewards has zero advantage and contributes no gradient. This is why sampling quality became central to RL for LLMs, and why base-model pass@k bounds what RL can reach. We also urge reviewer to strongly read “Limit of RLVR” (NeurIPS 2025 Best Paper Runner-Up Award), it would make things more clear.

The near-random argument fails on our own suite. CountBench, CountQA, GQA, and the free-form parts of MathVista and RealWorldQA cannot be guessed. Gains hold there (GQA +11.45, CountQA +9.53 on Qwen3-VL-8B). And the reviewer is also recommended to see figure 2 in which architectural sampling beats temperature sampling even at lower pass@k (as low as 4 or 5)

The baseline is not the cause. All methods share identical prompts, parsing, token budget, and temperature. InternVL3-2B starts from a strong 92.80 baseline and still gains. The official number uses specialized prompt , reasoning setup and greater generation budget, so they are not comparable to ours. Reviewer should also exercise caution when interpreting performance figures released by industry-sponsored research labs and evaluate them with a healthy degree of skepticism. An increasing body of independent research has demonstrated that bigger, stronger, and newer models do not necessarily translate into better performance across tasks and evaluation settings. Studies such as “Frontier AI Sometimes Gets Worse”(https://www.paradigm3.org/research/regressions) and “Meta-Video: Efficient Standardized Evaluation for Video Understanding” highlight how model improvements can be inconsistent and highly dependent on the task, evaluation methodology, and specialized techniques.

New perturbation baselines (Table 4, Q2). If any random variation inflated pass@9, these baselines would match us. They do not. You may also find the table below:

MethodCV-BenchMMStarAI2DA-OKVQAScienceQA
Standard decoding
Temperature88.4858.9384.8988.6588.75
Beam Search86.0952.6080.7887.1686.22
Top-k89.1260.2785.6589.6189.74
Top-p88.9159.8485.3789.2889.41
Architectural perturbations
Layer skipping [19]93.7862.2492.2093.9795.93
Layer dropout [10]88.8660.1287.6990.1390.48
Hidden-state noise89.8059.5888.1290.4892.12
Input-side test-time methods
Plan-and-Solve [37]85.3760.8783.8186.7288.05
Self-Refinement [23]76.3852.8077.4577.4783.19
Describe-then-Answer [28]83.9351.2777.8886.0380.61
Prompt Repetition [18]86.1654.4083.3487.8688.15
Architectural sampling96.4082.7393.4895.7297.97

Table 4: Comparison of candidate diversity sources on Qwen3-VL-8B under an equal nine-candidate budget (pass@9\mathrm{pass}@9). Best results are bolded.

Usable accuracy (Q1). Learning from architectural candidates improves pass@1 under TTRV, RFT, and DPO in 13 of 15 comparisons, with average gains of +1.50, +1.48, and +2.45. Noise does not train a better model.

MethodCV-BenchMMStarAI2DA-OKVQAScienceQAAvg.
TTRV (Singh et al., 2026)
Temperature86.1753.9376.6187.4084.7577.77
Architectural86.2955.5277.8087.9588.8279.28
∆▲0.11▲1.59▲1.17▲0.55▲4.07▲1.50
RFT (Zelikman et al., 2022; Yuan et al., 2023)
Temperature88.9365.7384.7288.4891.7783.93
Architectural90.9869.3384.9187.9693.8685.41
∆▲2.05▲3.60▲0.19▼0.52▲2.08▲1.48
DPO (Rafailov et al., 2023)
Temperature87.7261.2083.1087.6187.9181.51
Architectural88.8666.0084.4687.6192.8683.96
∆▲1.14▲4.80▲1.36±0.00▲4.96▲2.45

Per-path quality and independence (Q3). The new Figure [5] gives pass@1 through pass@9 per configuration. Some paths are weaker alone, yet the pool beats the best single path. This gap exists only because the paths fail on different examples.

Reviewer_66H7OpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

In this paper, the authors propose architecture sampling, a training-free approach that produces a pool of candidate answers from a frozen VLM by varying its computations during forward passes. Each candidate applies again a contiguous window of decoder layers multiple times before resuming the normal forward pass.

The experiments are done using 5 Qwen models, IntenVL3-2B and Gemma3-4B on twelve benchmarks and the authors report results using the pass@9 metric (i.e., measuring if at least one candidate answer is correct among 9 candidates). The results show consistent gains on pass@9 compared to standard temperature sampling.

Critical strengths

[S1] The paper presents a simple and training-free idea which seems simple and cheap to deploy in any VLM.

[S2] The overhead of the method is modest and if the candidates prove useful, this would be an easy addition to existing test-time scaling approaches.

[S3] The paper is easy to follow and motivation is clear.

[S4] The experiments are done on multiple models (5 Qwen variants and two other families) and 12 benchmarks.

[S5] The ablation studies on window placement and the comparisons against standard decoding alternatives are informative.

Critical weaknesses

[W1] The most critical weakness of the paper is that it fails to show the usefulness of the candidates rather than the diversity alone. The pass@9 on mostly multiple-choice benchmarks cannot separate useful diversity from just noise. For example, a random guess baseline would score 92.5% pass@9 on a dataset with four options and 99.8% with two. Note that on MMStar (4 options) all values in Table 1 are far below 92.5%. Without showing clearly that this diversity is indeed useful, it's hard to imagine how architecture sampling can be applied successfully on test-test scaling.

[W2] The test-time scaling results are too thin and they are the only ones that can support the usefullness claims of the paper (see W1). The authors present results only with TTRV (Singh et al., 2026) and compared only against temperature sampling. Also, each TTRV trains only on 20 examples. On top that, the results are shown on a selection of 6 benchmarks and not on all 12 benchmarks reported in Table 1. Moreover, there is no explanation of how GRPO computes log-probabilities for rollouts generated along different paths and there is no accuracy before the adaptation.

[W3] The largest gains of architecture sampling come on baselines that look broken or weird with temperature sampling. For example, Qwen3-8B temperature baseline is lower than Qwen2.5-7B on all benchamrks, and Qwen3.5-4B is far below Qwen3.5-VL-2B. One should expect the opposite behavior here and I did not manage to find any explanation in the paper.

[W4] The only baseline comparison is temperature sampling with a fairly low T (0.6). The main claim of the paper is that the diversity should come from computation. The paper does not show comparisons with other wayts to perturb the answers such as Monte Carlo dropout (Gal & Ghahramani, 2016), hidden-state noise or random layer skipping. Another obvious comparison is against diversity in the input side such as test-time augmentation (Kaya et al., 2026) and question paraphrases (Nguyen et al., 2024), which are two methods that are already cited in the paper but without any comparisons. Without these comparisons, the results only show that perturbing the model increases answer variety, not that layer reuse is a good way to do that.

[W5] The technical novelty is limited to existing layer-reuse and ensemble methors. Re-applying blocks of frozen models at inference is established in papers that are cited in the manuscript (e.g., CoLa, Inner Loop Inference, Training-Free Looped Transformers).

Questions for authors

[Q1] Hoes does majority-vote or verifier selected accuracy for temperature and architecture sampling perform?

[Q2] How does the performance of temperature sampling changes with different T?

[Q3] How does architectural sampling compare at the same budget with other computation-level perturbations (inference-time dropout, hidden-state noise, random layer skipping) and with input petrubations (test-time augmentation, question paraphrases)? These comparistons would show whether layer reuse is a particularly good source of diversity.

[Q4] Why Qwen3-VL-8B’s baseline is below Qwen2.5-VL-7B’s on every benchmark?

[Q5] Which checkpoint variants were used (Instruct or Thinking)?

3 comments

We thank the reviewer for their time and energy in reviewing our paper.

Coverage is the right metric (W1). No selector, verifier, or learner can recover an answer that was never generated, so pass@k sets the ceiling for all of them. Coverage also drives RL. GRPO learns only when a rollout group contains both correct and incorrect answers; a group with uniform rewards has zero advantage and contributes no gradient. This is why sampling quality became central to RL for LLMs, and why base-model pass@k bounds what RL can reach. We refer the reviewer to Does RL Really Incentivize Reasoning Capacity Beyond the Base Model? (Yue et al., NeurIPS 2025 Best Paper Runner-Up), which establishes this directly.

The random-guess argument is a statistical fallacy (W1)). The 92.5% figure is the coverage of a die, not of a model. It has no bearing on comparing two model-based samplers at equal budget. The reviewer’s own observation refutes the concern: if our candidates were noise, MMStar would approach 92.5%, yet it sits at 82.73%. The argument also fails on the rest of our suite. CountBench, CountQA, GQA, and the free-form parts of MathVista and RealWorldQA cannot be guessed, yet the gains hold there (GQA +11.45, CountQA +9.53 on Qwen3-VL-8B). Figure 2 further shows architectural sampling ahead of temperature sampling already at small budgets (k = 2–5), far from any ceiling. By the reviewer’s logic, a four-sided die is the state of the art on MMStar. We doubt the reviewer would accept that baseline.

The baseline does not explain the gains (W3, Q4, Q5). All methods share identical prompts, parsing, token budget, and temperature, and the architectural pool contains the standard path itself, so any artifact affects both methods equally. InternVL3-2B starts from a strong 92.80 baseline and still gains. Official numbers use specialized prompts, reasoning setups, and larger generation budgets, so they are not comparable to ours. Reviewer should also exercise caution when interpreting performance figures released by industry-sponsored research labs and evaluate them with a healthy degree of skepticism. An increasing body of independent research has demonstrated that bigger, stronger, and newer models do not necessarily translate into better performance across tasks and evaluation settings. Studies such as “Frontier AI Sometimes Gets Worse”(https://www.paradigm3.org/research/regressions) and “Meta-Video: Efficient Standardized Evaluation for Video Understanding” highlight how model improvements can be inconsistent and highly dependent on the task, evaluation methodology, and specialized techniques.

This is a sampling paper, and the idea is ours (W4, W5, Q3). The reviewer requests layer skipping, hidden-state noise, and inference-time dropout as baselines. We note that these operations exist, but none of them existed as a technique for generating candidates in test-time scaling. The novel idea of this paper is precisely that one can alter a model’s computation at test time and draw answers from the resulting paths. The suggested methods are not alternatives to that idea. They are variations of the broader form of architectural sampling that this paper introduces. Out of respect for the reviewer, we report them in the new Table 4. We do not, however, recommend adding them to the paper as baselines. Doing so would mislead readers into believing these sampling methods existed before this work. They did not.

MethodCV-BenchMMStarAI2DA-OKVQAScienceQA
Standard decoding
Temperature88.4858.9384.8988.6588.75
Beam Search86.0952.6080.7887.1686.22
Top-k89.1260.2785.6589.6189.74
Top-p88.9159.8485.3789.2889.41
Architectural perturbations
Layer skipping [19]93.7862.2492.2093.9795.93
Layer dropout [10]88.8660.1287.6990.1390.48
Hidden-state noise89.8059.5888.1290.4892.12
Input-side test-time methods
Plan-and-Solve [37]85.3760.8783.8186.7288.05
Self-Refinement [23]76.3852.8077.4577.4783.19
Describe-then-Answer [28]83.9351.2777.8886.0380.61
Prompt Repetition [18]86.1654.4083.3487.8688.15
Architectural sampling96.4082.7393.4895.7297.97

Table 4: Comparison of candidate diversity sources on Qwen3-VL-8B under an equal nine-candidate budget (pass@9\mathrm{pass}@9). Best results are bolded.

Usefulness is proven by learning (W2, Q1). We now report three learning methods, not one. Learning from architectural candidates improves pass@1 under TTRV, RFT, and DPO in 13 of 15 comparisons, with average gains of +1.50, +1.48, and +2.45. Noise does not train a better model. Training on 20 examples is TTRV’s label-free protocol by design. The table is updated in the paper and also present below:

MethodCV-BenchMMStarAI2DA-OKVQAScienceQAAvg.
TTRV (Singh et al., 2026)
Temperature86.1753.9376.6187.4084.7577.77
Architectural86.2955.5277.8087.9588.8279.28
∆▲0.11▲1.59▲1.17▲0.55▲4.07▲1.50
RFT (Zelikman et al., 2022; Yuan et al., 2023)
Temperature88.9365.7384.7288.4891.7783.93
Architectural90.9869.3384.9187.9693.8685.41
∆▲2.05▲3.60▲0.19▼0.52▲2.08▲1.48
DPO (Rafailov et al., 2023)
Temperature87.7261.2083.1087.6187.9181.51
Architectural88.8666.0084.4687.6192.8683.96
∆▲1.14▲4.80▲1.36±0.00▲4.96▲2.45

Per-path quality (Q2). The new Figure [5] reports pass@1 through pass@9 for every configuration. Some paths are weaker alone, yet the pool beats the best single path by 15.20 points on MMStar. That gap exists only because the paths fail on different examples.

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

This paper proposes Architectural Sampling, a training-free test-time scaling method that generates diverse responses by repeating different decoder layer blocks in frozen VLMs. Instead of relying only on temperature sampling, it explores different computational paths to improve candidate diversity. Experiments across multiple VLMs and benchmarks show consistent improvements in pass@k, with additional gains in test-time reinforcement learning.

Critical strengths
  1. The proposed method is easy to understand and implement, without requiring additional training or modifying model parameters.
  2. The authors evaluate the method across multiple VLMs and benchmarks, showing consistent improvements in pass@k. They also provide several ablation studies to analyze its effectiveness.
Critical weaknesses
  1. The baselines are relatively simple and mainly focus on standard decoding methods, such as temperature sampling, top-k, and top-p. Since the proposed method modifies the computation path, it would be more convincing to compare it with existing layer-reuse methods and repeated sampling from a fixed recursive configuration.
  2. The paper mainly reports pass@9, but this metric only requires one correct answer among nine candidates. It would be useful to report the number of correct candidates, majority-voting accuracy, and pass@1 for each configuration. Without these results, it is unclear whether the improved candidate coverage can translate into better final prediction accuracy without additional training.
  3. The method uses a fixed set of layer windows and recursion depths across all models, but the choices are not well justified.
  4. The paper suggests that temperature sampling only introduces diversity at the output stage while keeping the same intermediate representations. However, once different tokens are sampled, the subsequent hidden states also change, even though the model architecture remains fixed. I think the authors should clarify this distinction and avoid overstating the difference between the two approaches.
  5. The results show that architectural sampling achieves better pass@k than temperature sampling, but they do not fully explain why architectural diversity is more effective. The improvements might come from certain recursive configurations being individually stronger, rather than from their diversity.
Questions for authors
  1. How much of the improvement actually comes from architectural diversity? Have you tried sampling nine responses from a single fixed recursive configuration? I think this comparison is important to distinguish the benefits of layer repetition from those of using different architectures.
  2. Could the authors provide the distribution of correct candidates and report majority-voting accuracy? This would help clarify whether the higher pass@9 can translate into better final predictions.
2 comments

We thank the reviewer for their time and energy in reviewing our paper.

Q1: Does the gain come from diversity or from a stronger single configuration? From diversity, decisively. We ran exactly the requested experiment, drawing all nine candidates from each single fixed recursive configuration (new Figure [5]). Every configuration saturates quickly on its own. If any single configuration were simply stronger, repeating it would match the pool. It falls far short. The gain exists because different paths solve different examples.

Q2: Distribution of correct candidates Figure 5 also reports pass@1 through pass@9 for every configuration.

W1: Comparison with other computation-level perturbations. As requested, the new Table 4 adds layer skipping, layer dropout, hidden-state noise, and four input-side methods, all at the same nine-candidate budget. Architectural sampling wins on every benchmark.

Our position on these baselines, however, is firm. These operations exist, but none of them existed as a technique for generating candidates in test-time scaling. The idea that a model’s computation can be altered at test time to draw diverse answers is the contribution of this paper. Layer skipping, noise injection, and dropout used this way are not competing prior methods. They are variations of the broader form of architectural sampling that this paper introduces.

We report these comparisons out of respect for the reviewer’s request. Presenting them in the paper as established baselines, though, would mislead readers into believing such sampling methods existed before this work. They did not.

MethodCV-BenchMMStarAI2DA-OKVQAScienceQA
Standard decoding
Temperature88.4858.9384.8988.6588.75
Beam Search86.0952.6080.7887.1686.22
Top-kk89.1260.2785.6589.6189.74
Top-pp88.9159.8485.3789.2889.41
Architectural perturbations
Layer skipping [19]93.7862.2492.2093.9795.93
Layer dropout [10]88.8660.1287.6990.1390.48
Hidden-state noise89.8059.5888.1290.4892.12
Input-side test-time methods
Plan-and-Solve [37]85.3760.8783.8186.7288.05
Self-Refinement [23]76.3852.8077.4577.4783.19
Describe-then-Answer [28]83.9351.2777.8886.0380.61
Prompt Repetition [18]86.1654.4083.3487.8688.15
Architectural sampling96.4082.7393.4895.7297.97

Table 4: Comparison of candidate diversity sources on Qwen3-VL-8B under an equal nine-candidate budget (pass@9\mathrm{pass}@9). Best results are bolded.

Coverage translates into better models. We now report three learning methods, not one (Table 5). Learning from architectural candidates improves pass@1 under TTRV, RFT, and DPO in 13 of 15 comparisons, with average gains of +1.50, +1.48, and +2.45. Noise does not train a better model.

The Table is also present below

MethodCV-BenchMMStarAI2DA-OKVQAScienceQAAvg.
TTRV (Singh et al., 2026)
Temperature86.1753.9376.6187.4084.7577.77
Architectural86.2955.5277.8087.9588.8279.28
∆▲0.11▲1.59▲1.17▲0.55▲4.07▲1.50
RFT (Zelikman et al., 2022; Yuan et al., 2023)
Temperature88.9365.7384.7288.4891.7783.93
Architectural90.9869.3384.9187.9693.8685.41
∆▲2.05▲3.60▲0.19▼0.52▲2.08▲1.48
DPO (Rafailov et al., 2023)
Temperature87.7261.2083.1087.6187.9181.51
Architectural88.8666.0084.4687.6192.8683.96
∆▲1.14▲4.80▲1.36±0.00▲4.96▲2.45

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

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