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Under review as a conference paper at ICLR 2027

Linear-Cost Unsupervised Elicitation from Pretrained Language Models

Abstract

Post-training language models depend on human annotators for labels, which becomes a bottleneck as models grow more capable: annotation becomes unreliable as tasks outpace human expertise. Unsupervised elicitation avoids that by drawing labels from the pretrained model itself. Internal Coherence Maximization (ICM) is one such method; it approaches golden-supervision accuracy across a range of labeling tasks. However, its simulated-annealing search over mutual predictability requires forward passes, hours for a few hundred examples, and per-dataset hyperparameter tuning. We show this search is largely unnecessary. Our method, Linear-Cost Unsupervised Elicitation (LC-UE), replaces it with two inexpensive phases. The first phase labels each group in order of the model's zero-shot confidence, conditioning only on the groups labeled before it, which optimizes an autoregressive form of coherence rather than mutual predictability itself. The second phase closes that gap with a few refinement sweeps, scoring candidate label flips under a cheap proxy against a frozen context and verifying each sweep with one exact computation. Both phases satisfy the task's consistency constraints by construction. Across TruthfulQA, GSM8K-verification, Alpaca, and two pluralistic alignment benchmarks, LC-UE matches or outperforms ICM and few-shot bootstrapping at cost for , with no per-dataset tuning. On TruthfulQA (), this amounts to an estimated fewer forward passes than ICM, and at least fewer even under a conservative bound. Taken together, LC-UE makes unsupervised elicitation practical at scale and across diverse tasks, without the computational cost or per-dataset tuning that has limited prior methods.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Unsupervised Elicitation, Scalable Oversight

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

This paper works on unsupervised elicitation: inferring labels for a set of binary training claims (e.g., whether a math solution is correct, or whether one response is more helpful than another) purely from a pretrained base model’s own log-probabilities, with the aim that these self-generated labels, when used as many-shot demonstrations, yield test accuracy close to that obtained with ground-truth-labeled demonstrations. Previous methods, such as Internal Coherence Maximization (ICM), use simulated annealing under logical-consistency constraints to search for the labeling that maximizes mutual predictability, the summed log-probability of each label when all other labeled examples are given in context. The authors argue that since changing any one label alters the context of every term, each search step must rescore the entire labeled set, making ICM roughly quadratic in forward passes and dependent on per-dataset hyperparameter tuning, while simpler bootstrapping methods are linear but drop the mutual-predictability objective altogether. To address this, they propose Linear-Cost Unsupervised Elicitation (LC-UE), which first labels consistency groups in one single pass ordered by zero-shot confidence, each conditioned on all previously labeled groups, and then runs a few refinement sweeps in which label changes for every group are proposed in parallel from their direct effect on mutual predictability against a frozen context, with a sweep kept only if one exact recomputation of mutual predictability confirms an improvement; logical consistency is enforced as a hard constraint in both phases. The authors derive a total cost of n(3+2K)n(3+2K) forward passes for nn claims and KK sweeps, with sweeps stopping after two to three on average. Across five benchmarks (TruthfulQA, GSM8K-verification, Alpaca, GlobalOpinionQA, and OpinionQA) with Llama 3.1 8B and 70B base models, they report many-shot test accuracy that matches or exceeds ICM and two iterative-bootstrapping variants, using an estimated 228–555× fewer forward passes than ICM on the three larger training sets.

Critical strengths
  1. Targets a real and interesting bottleneck of unsupervised elicitation. The quadratic cost of ICM is resource-intensive: it is corroborated by Shrivastava et al. (2026), Mahbub et al. (2026), and the authors' own controlled run, in which ICM at n=256n=256 ran for over five hours and labeled only 101 of 256 claims on the same hardware where the full LC-UE pipeline finishes in under an hour (Section 4.2, Figure 4).
  2. A simple, well-reasoned design. The method follows directly from a clear diagnosis of why mutual predictability is expensive: the paper separates the direct effect of a group's labels on its own terms from the indirect effect on every other claim's context, scores only the former against a frozen snapshot, and uses a single exact recomputation per sweep as a safeguard (Section 3.3).
  3. Transparent cost accounting. The cost derivation n(3+2K)n(3+2K) is explicit, and the reported reduction factors can be reproduced from the stated values of rr, nn, and KK (Section 3.4). The authors count the final, discarded sweep toward cost rather than only accepted sweeps, report a conservative bound at the sweep cap K=5K=5 alongside the realized cost, and explain why the n=2,604n=2{,}604 run is cheaper than the n=1,024n=1{,}024 run (Section 4.2).
  4. Experimental results are significant. The evaluation spans verification, truthfulness, pairwise preference, and two pluralistic-alignment benchmarks. Across all five benchmarks, LC-UE's accuracy is at or above the ICM numbers it is compared against.
Critical weaknesses
  1. The paper motivates itself with post-training but never shows that its labels are useful for it. The abstract opens with “Post-training language models depend on human annotators for labels, which becomes a bottleneck as models grow more capable,” and the introduction and conclusion keep this framing. Yet no experiment post-trains anything; the inferred labels are only used as in-context demonstrations, and the reported metric is how close this gets to many-shot prompting with gold labels. I suggest either adding a fine-tuning experiment with LC-UE labels or rewriting the abstract and introduction around in-context label inference.
  2. It is unclear whether keeping mutual predictability is what makes LC-UE better than bootstrapping. The paper's main distinction from Shrivastava et al. (2026) is that it restores the MP objective, yet Phase 1 alone, which does not use MP, combines confidence ordering, bootstrapping, and hard consistency, whereas each of the two bootstrap baselines uses only one of the first and the last. Phase 1 results are shown only in Figure 5b for two benchmarks, without exact numbers; reading the bars, Phase 1 alone already reaches about 71.6 on GSM8K-verification and 87.0 on TruthfulQA, above both bootstrap baselines (71.1 and 86.1), and Phase 2 adds only about 0.2 points on GSM8K-verification. The gains over bootstrapping may therefore come from combining these components rather than from MP.
  3. The baseline comparisons are not run under matched conditions. The ICM numbers on three benchmarks are copied from Wen et al. (2025a) rather than re-run, with a different TruthfulQA training set (2,604 vs. 2,560 claims) and possibly a different prompt template (see Q1), while the bootstrap baselines are re-run with unspecified settings and fall unusually far below ICM on OpinionQA (71.4 vs. 82.2), unlike the near-ICM results Shrivastava et al. (2026) report elsewhere (see Q2). In addition, all results come from a single run, and the error bars in Figure 3 are not explained, so several margins of one point or less (e.g., 0.8 over Confident Bootstrap on GSM8K-verification, 0.5 and 0.1 over ICM on GOQA and OpinionQA) cannot be judged.
  4. The cost comparison uses an unequal unit and the wrong reference point. The forward passes are counted assuming they cost the same, but Phase 1 reuses a KV cache and processes only each new group, whereas every Phase 2 pass processes up to 1,302 demonstrations from scratch (Appendix G), and the ICM counts are extrapolated from an iterations-per-datapoint value rr measured at n=128n=128 to n≈2,600n\approx2{,}600. More importantly, the headline 228–555× reductions are relative to ICM, while the relevant comparison is bootstrapping, which is also linear; the caption of Figure 1b itself notes that the bootstrap variants use shorter contexts and hence less compute, yet their cost is never reported.
Questions for authors
  1. Do LC-UE's prompts use the same template as the ICM results you compare against? The ICM numbers on three benchmarks are copied from Wen et al. (2025a), whose reference prompt ends with a trailing space that Shrivastava et al. (2026) report can depress Llama's accuracy, and Appendix C does not say whether LC-UE's prompts share it. If they do not, part of the margin over ICM (e.g., +3.0 on GSM8K-verification, +4.0 on Alpaca) may come from prompt formatting rather than the method. Could the authors report LC-UE under the original template, or re-run ICM under yours at n=256n=256 as you already did in Section 4.2?
  2. What settings were used for the re-run bootstrap baselines? LC-UE uses 2,560 / 256 / 160 test-time demonstrations on TruthfulQA / GSM8K-verification / Alpaca and 20 on GOQA/OQA, whereas Shrivastava et al. (2026) evaluate with 128 shots. Please state the test-time demonstration counts, subset sizes, and number of rounds for both bootstrap variants, especially on OpinionQA, where Consistent Bootstrap (71.4) falls far below ICM (82.2). If these differ from LC-UE's, could you report the baselines under matched settings? Otherwise, the comparison with baselines could be unfair.
  3. Why is it worth keeping mutual predictability as the objective? The paper’s motivation is to keep ICM’s MP objective while removing its search, but it offers little evidence that optimizing MP improves accuracy. Phase 1, which does not use MP, already achieves: in Figure 5b, Phase 2 adds about 2.7 points on TruthfulQA, but only about 0.2 on GSM8K-verification, and no Phase 1 results are shown for the other three benchmarks. Could you report the exact Phase 1-only test accuracy on all five benchmarks, or otherwise explain why MP should help beyond confidence-ordered bootstrapping with hard consistency?
3 comments
AuthorsOpenReview ↗

Response (1/2)

We thank the reviewer for the careful and constructive review. We answer the questions first, then address the remaining weaknesses.

Q1. Do LC-UE's prompts use the same template as ICM?

Yes. LC-UE uses exactly the same prompt templates as the original ICM implementation (Wen et al., 2025a), including the trailing space the reviewer mentions. Any effect of prompt formatting therefore applies equally to both methods and cannot explain the margins over ICM.

The one remaining difference is that our TruthfulQA training set has 2,604 claims instead of 2,560. At test time, though, we use 2,560 labeled demonstrations, as ICM does. For a fully controlled comparison, we also ran ICM ourselves at 256 claims, with the same model, hardware, and prompts as LC-UE (Section 4.2).

Q2. What settings were used for the bootstrap baselines?

All methods, including both bootstrap baselines, use the same number of test-time demonstrations: 2,560 on TruthfulQA, 256 on GSM8K-verification, 160 on Alpaca, and 20 on GlobalOpinionQA and OpinionQA.

For the bootstrap baselines themselves, we followed Shrivastava et al. (2026): subsets of 512 examples and three rounds of labeling (0-shot, then 8-shot, then 128-shot). For the confident bootstrap, the demonstrations carried between rounds are limited to the 64 most confident True and 64 most confident False predictions. For the consistent bootstrap, the consistency rules are applied to each round's predictions. The revised version describes these settings in full (Appendix C.3).

We used these same settings on every benchmark, so the larger gap between the bootstrap baselines and ICM on OpinionQA is not due to different tuning. We do not yet have a full explanation for it.

Q3. Why keep mutual predictability as the objective? (also W2)

We agree with the reviewer's reading. Much of LC-UE's advantage over the bootstrap baselines comes from combining bootstrapping with hard consistency constraints in a single pass, not from mutual predictability alone. Here are the exact Phase 1 results on all five benchmarks (Table 13, Appendix I):

DatasetPhase 1 onlyPhase 1 + Phase 2Change
TruthfulQA87.089.7+2.7
GSM8K-verification71.671.9+0.3
Alpaca65.266.2+1.0
GlobalOpinionQA72.772.9+0.2
OpinionQA81.982.3+0.4

Phase 2's gains are modest and vary by dataset. We still think it is worth keeping, for three reasons:

  1. It never hurts. A sweep is kept only if exact mutual predictability improves, and on all five benchmarks the refined labels never scored below the Phase 1 labels on test accuracy.
  2. It gives a label-free check. Mutual predictability can be computed without any ground truth, so each accepted change is verified to improve coherence. Bootstrapping has no comparable signal.
  3. It can help substantially. On TruthfulQA and GSM8K-verification, it closes most of the remaining gap to gold labels, and on TruthfulQA it adds 2.7 points, which is what lifts LC-UE above ICM.

In the revised version, we have reframed the contribution to match (Section 1 and Section 5.2): a linear-cost method that combines these components and adds a verified refinement step, rather than a claim that mutual predictability is the main source of the gains.

AuthorsOpenReview ↗

Response (2/2)

W1. The post-training framing.

We agree. In the revised version, we have rewritten the abstract and introduction around in-context label inference and listed fine-tuning as a limitation (Section 6). Our response to Reviewer JYC4 gives further evidence on the quality of the full labeled set, including training-set label accuracy.

W3. Single runs and error bars.

The error bars in Figure 3 show the standard deviation over three evaluation runs on the test set, all using the same elicited labels. Although scoring uses temperature 0, GPU inference is not perfectly deterministic, so test predictions vary slightly between runs. These error bars therefore capture only evaluation noise, not variation in the labels themselves. The reviewer is right that each set of labels comes from a single run of the pipeline, and we have stated this clearly in the revised caption of Figure 3.

Our new ordering experiments give a sense of how much the labels themselves vary between runs. Across independent Phase 1 runs with different random orders, test accuracy had a standard deviation of 0.2 to 1.3 points on Alpaca, GSM8K-verification, and TruthfulQA (Table 12, Appendix H; see also our response to Reviewer JYC4). Given variation of this size, we agree that margins of one point or less should be read as ties, not improvements.

W4. The cost comparison.

We agree on both points.

First, forward passes are not all equal, so we measured cost directly. All runs below are on TruthfulQA with 2× RTX PRO 6000 GPUs:

MethodnWall-ClockGPU-hours
LC-UE2560.84 h1.7
ICM (measured; labeled only 101 of 256 claims)256> 5.07 h> 10.1
Confident bootstrap2,6040.15 h0.3
Consistent bootstrap2,6040.15 h0.3
LC-UE2,6044.50 h9.0
ICM (extrapolated from n = 256)2,604~525 h~1,050

Measured this way, LC-UE is about 117× faster than our extrapolated ICM cost at 2,604 claims, and at least 6× faster at 256 claims, where ICM did not even finish. These ratios are smaller than the forward-pass ratios in the paper, and we have added wall-clock time and GPU-hours to the revised version (Section 4.2, Table 1).

Second, the reviewer is right that bootstrapping is the more relevant comparison. Both bootstrap variants are also linear, and LC-UE costs about 30× more than they do. That extra cost is the price of the refinement step, and Q3 shows what it buys. LC-UE's large cost advantage is therefore over ICM only, and we have made this explicit in the revised version (Section 4.2).

On the ICM estimates: as the reviewer notes, the iterations-per-datapoint value r was measured at 128 claims. However, in our own run at 256 claims, ICM had labeled only 101 claims after the number of iterations that r predicts. If anything, our extrapolated costs underestimate ICM's true cost.

Thank you for your response. I consider Phase 2 to be the most important and novel component of the proposed design. However, the performance gains attributable to Phase 2 appear modest, though it consistently avoids performance degradation. I believe the author should provide a clearer explanation of when and why Phase 2 yields significant performance gains on some tasks but not others, such as GlobalOpinionQA, where phase 2 only improves by 0.2. Therefore, I will maintain my score.

Reviewer_NzefOpenReview ↗
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Paper summary

The paper proposes using LLM for annotation as alternative of crowdsourcing or human expertise. Unsupervised Elicitation (LC-UE) combines confidence-ordered labeling with greedy mutual-predictability refinement under logical consistency constraints.

Author claimed that Linear-Cost Unsupervised Elicitation (LC-UE) can matche or outperforms ICM and few-shot bootstrapping at cost for with no per-dataset tuning. On TruthfulQA this amounts to an estimated 456 times fewer forward passes than ICM, and at least 250 times fewer even under a conservative bound. The paper mainly compares against Internal Coherence Maximization (ICM) and iterative bootstrapping across five benchmarks ( GSM8K-verification, TruthfulQA, Alpaca, GlobalOpinionQA (GOQA), OpinionQA (OQA)). The main evaluation metric is test accuracy using many-shot prompting with the elicited labels.

Critical strengths
  • Interesting research topic : The paper addresses an important research problem by exploring how LLMs can generate annotations without human supervision, potentially reducing annotation costs and improving scalability.

  • Computational Efficiency: The paper claimed that it reduced the number of forward passes by approximately 465 times (TruthfulQA) and 555 times (GSM8K-verification) compared to ICM.

Critical weaknesses

Narrow Comparative Scope

The paper closely associates its motivation, baseline comparisons, and framing with Internal Coherence Maximization (ICM). The authors should better contextualize their work within the broader landscape of consistency-based and cross-model consistency methods, either as empirical comparisons or within the related work.

Context Window Truncation Alters Objective

Equation (1) shows full mutual predictability, however Phase 2 use heavily truncated contexts.

Reliance on Unverified, Informal Baselines

The manuscript relies heavily on an informal LessWrong blog post (Shrivastava et al., 2026, "Eliciting base models with simple unsupervised techniques") to establish its iterative bootstrapping baseline and motivate its methodological improvements. This source has not been formally published or peer-reviewed, and it does not show in standard academic indices. I think ICLR submission need to evaluate its core contributions against established, formally verified literature. I have found similar paper [2] but the author list does not contain Tianyi Alex Qiu. I am not sure why author did not cite the [2] directly. It makes me less confident about the paper.

Ground-Truth Leakage

TruthfulQA uses gold-derived consistency partitions. Can the authors provide leakage-free experiments to establish the effectiveness of genuinely unsupervised elicitation?

Efficiency and Experimental Fairness

The reported speedups are primarily based on forward-pass counts rather than matched end-to-end computational costs. In addition, several ICM results are reused from prior work. More controlled comparisons using identical context budgets, prompts, and computational resources are required.

[1] Aditya Shrivastava, Allison Qi, Callum Canavan, Tianyi Alex Qiu, Jonathan Michala, and Fabien Roger. Eliciting base models with simple unsupervised techniques. LessWrong, 2026. URL https://www.lesswrong.com/posts/rFxfMbwJ3v4PNesWP. Accessed: 2026-09- 11.

[2] Callum Canavan, Aditya Shrivastava , Allison Qi, Jonathan Michala, Fabien Roger. Three Concrete Challenges and Two Hopes for the Safety of Unsupervised Elicitation

Questions for authors

1.How does the truncated-context objective relate to full mutual predictability, and how sensitive are the results to the truncation strategy?

2.Does Figure 5(a) represent independent algorithm runs under different orders, or merely different orderings of identical predictions?

3.What is the improvement over independent consistency-constrained relabeling using the same confident demonstrations and inference budget?

4.Why does the Phase 1 group-selection rule maximize individual-claim confidence rather than the group-level objective?

5.Are ICM and LC-UE compared using identical prompts, context limits, scoring rules, and test configurations?

6.How well does the method perform without gold-derived consistency constraints on TruthfulQA?

7.What theoretical properties, beyond monotonic improvement of the capped objective, can be established for Phase 2?

4 comments
AuthorsOpenReview ↗

Response (1/3)

We thank the reviewer for the detailed questions. We answer them in order below, then address the related work and citation concerns.

Q1. How does the truncated-context objective relate to full mutual predictability, and how sensitive are the results to the truncation strategy?

In short, the two are the same whenever no truncation is needed, and truncation has little effect when we do use it.

When there is no truncation. If all labeled examples fit within the limit, we compute full mutual predictability exactly. This covers TruthfulQA up to 1,302 claims, and GlobalOpinionQA and OpinionQA at every size. Figure 6 shows full mutual predictability at these sizes, and Phase 2 improves it in every case.

When we do truncate. This happens in two cases:

  • GSM8K-verification and Alpaca. Each example is long (a full math solution, or two complete responses), so only a few hundred fit in the model's context window. Any method has to truncate here, including ICM.
  • TruthfulQA at the full 2,604 claims. Here, all labels do fit. Phase 1 uses all of them, because it builds the context step by step and can reuse what it has already processed. Phase 2 cannot do this: each claim is scored against a different set of other labels, so every call would have to process all 2,604 labels from scratch, which is too slow. So we limit Phase 2 to 1,302 labels (Appendix G).

In both cases, we use the same limit when checking whether a sweep improved the objective, so before-and-after comparisons are always fair.

How sensitive are the results? We tested this on TruthfulQA by lowering the Phase 2 limit from 1,302 to 1,024 labels. Test accuracy went from 89.7% to 89.4%, a drop of only 0.3 points, so the results do not depend much on the exact limit. In the revised version, we have added this comparison to Appendix G, which also explains what the objective measures under truncation: how well the most confident labels predict all the others. If the reviewer finds it useful, we are happy to test more limits, including no truncation at all, in the final version.

Q2. Does Figure 5(a) represent independent algorithm runs under different orders, or merely different orderings of identical predictions?

They are independent runs, and we clarify this in the updated caption. The two curves come from separate Phase 1 runs on the same 256 TruthfulQA claims, one in confidence order and one in random order, and show training-label accuracy as each run proceeds. The caption says the curves end at the same point "by construction," which is incorrect. They end at nearly the same point (about 85%) because both orders produce labels of similar quality, not because of how the figure is built.

Figure 5a was still limited: it used one random seed, showed training accuracy only, and had no reverse order. So we ran a fuller version, rerunning Phase 1 in confidence order, random order (three seeds), and reverse confidence order on Alpaca, GSM8K-verification, and TruthfulQA at full size. The full results are in our response to Reviewer JYC4 and in Appendix H (Table 12).

The order barely matters. On all three datasets, test accuracy varies by less than one point across orders, and no order is consistently best. On TruthfulQA, for example, confidence, random, and reverse order reach 87.0%, 87.4 ± 0.2%, and 87.6%.

In the revised version, we have replaced Figure 5a with the TruthfulQA results, added the Alpaca and GSM8K-verification results to Appendix H, corrected the caption, and revised the related claims in Sections 3.2 and 5.1 (highlighted in blue).

AuthorsOpenReview ↗

Response (2/3)

Q3. What is the improvement over independent consistency-constrained relabeling using the same confident demonstrations and inference budget?

Our Phase 1 is essentially this procedure: it labels each group under the consistency rules, using the most confident labels as demonstrations. On GSM8K-verification and Alpaca, the match is exact for most examples: once the labeled set passes the context limit, the demonstrations become a fixed set of the most confident labels. On TruthfulQA and the opinion datasets, Phase 1 instead uses all previously labeled groups as demonstrations.

So what LC-UE adds over this procedure is Phase 2 (Table 13, Appendix I):

DatasetPhase 1 onlyPhase 1 + Phase 2Change
TruthfulQA87.089.7+2.7
GSM8K-verification71.671.9+0.3
Alpaca65.266.2+1.0
GlobalOpinionQA72.772.9+0.2
OpinionQA81.982.3+0.4

Phase 2 never lowers test accuracy, but its gain is modest: 2.7 points on TruthfulQA, and between 0.2 and 1.0 points elsewhere. For reference, the consistent bootstrap baseline, which labels each example independently and applies the consistency rules afterward, scores below Phase 1 on all five benchmarks (Figure 3).

On the inference budget: this comparison is not budget-matched. Phase 2 costs about 2Kn extra forward passes for K refinement sweeps, and we have not tested whether spending the same compute on additional relabeling rounds would do as well. We have noted this as a limitation in the revised version (Section 6).

Q4. Why does the Phase 1 group-selection rule maximize individual-claim confidence rather than the group-level objective?

On three of our five benchmarks, the two rules are the same. On Alpaca, GlobalOpinionQA, and OpinionQA, each group has two claims, and exactly one must be true. Write each claim's score as ℓ = log P(True) − log P(False). The difference in total group likelihood between the two possible labelings is then exactly ℓ_a − ℓ_b, so picking the claim with the higher score is the same as picking the labeling with the higher group likelihood.

On GSM8K-verification and TruthfulQA, groups are larger, and the two rules can give different answers. There, Phase 1's rule is a simple heuristic. We chose it because it follows the consistency projection used by the consistent bootstrap baseline (Shrivastava et al., 2026), in which the highest-scoring claim in a group determines the rest. This keeps Phase 1 directly comparable to that baseline. Phase 2 then revisits every group using the full group-level objective (Eq. 2), so any group where the heuristic chose a lower-likelihood labeling can still be corrected.

Using the group-level rule directly in Phase 1 would cost no extra forward passes, since it uses the same claim scores. If the reviewer finds it useful, we are happy to report this variant in the final version.

Q5. Are ICM and LC-UE compared using identical prompts, context limits, scoring rules, and test configurations?

For TruthfulQA, GSM8K-verification, and Alpaca, we reuse the ICM numbers reported by Wen et al. (2025a). We use the same base models, task setup, data splits, scoring method, and prompt templates as the original ICM implementation. The one difference is that our TruthfulQA training set has 2,604 claims instead of 2,560; at test time, we use 2,560 labeled demonstrations, as ICM does. All methods, including the bootstrap baselines, use the same number of test-time demonstrations: 2,560 on TruthfulQA, 256 on GSM8K-verification, 160 on Alpaca, and 20 on GlobalOpinionQA and OpinionQA. For GlobalOpinionQA and OpinionQA, we ran ICM ourselves following Mahbub et al. (2026). The revised version describes the bootstrap settings in full (Appendix C.3) and reports measured wall-clock time and GPU-hours for all methods (Section 4.2, Table 1; see also our response to Reviewer vpPQ).

AuthorsOpenReview ↗

Response (3/3)

Q6. How well does the method perform without gold-derived consistency constraints on TruthfulQA?

This is a fair concern, and we run an experiment to answer this empirically.

First, some context: the leak only affects TruthfulQA. On the other four benchmarks, the consistency rules come from the claims themselves, not from labels. On GSM8K-verification, solutions that reach the same final answer must get the same label. On Alpaca, one of the two responses must win. On GlobalOpinionQA and OpinionQA, one answer option must win. LC-UE matches or beats ICM on all four. We kept the partition on TruthfulQA only because ICM's reported numbers use it too, and dropping it would have made our comparison unfair to ICM.

To answer the reviewer's question directly, we reran LC-UE on TruthfulQA without the partition. Each claim is now labeled on its own, with no consistency rules, and Phase 2 simply considers flipping individual labels using the same objective as before:

MethodUses gold partition?Test acc.
Zero-shot (base model)–60.2
LC-UENo83.7
Confident bootstrapNo84.3
LC-UEYes89.7
Many-shot with gold labels–91.0

Without the partition, LC-UE reaches 83.7%. That still closes 76% of the gap between zero-shot prompting and prompting with gold labels, and it is on par with the confident bootstrap, the strongest baseline that also avoids the leak.

Clear takeaway: on TruthfulQA, LC-UE's advantage over the baselines comes from the partition. ICM's 88.0% relies on the same partition, and there is no leak-free ICM result to compare against, so our claim of matching or beating ICM rests on the other four benchmarks. In the revised version, we have added the leak-free result to Section 4.1 and the limitations (Section 6), and stated this explicitly.

Q7. What theoretical properties, beyond monotonic improvement of the capped objective, can be established for Phase 2?

We can show four properties:

  1. Every labeling is valid. Phase 2 only ever moves between labelings that satisfy the consistency rules, so it can never produce an inconsistent one.
  2. Phase 2 always finishes. Only a limited number of valid labelings exist, and each accepted sweep strictly improves the score. So Phase 2 can never return to a labeling it has already left, and it must eventually stop.
  3. For most groups, the cheap estimate is exact. The estimate ignores how changing one group's labels affects the other claims. For groups outside the truncation limit, that effect is zero, because their labels never appear in any other claim's context (Appendix G). So for these groups, the estimate is exactly right.
  4. Sometimes the result is locally optimal. If a sweep finds no changes worth making, then no single change to any group outside the limit could improve the score. However, Phase 2 usually stops for a different reason (a sweep fails the final check), and in that case this guarantee does not apply.

Related work (W1).

Appendix B situates our work within the broader landscape the reviewer mentions: methods that rely on consistency alone (CCS by Burns et al., 2022, and the critique by Farquhar et al., 2023), self-consistency, confidence-based training signals, weak-to-strong generalization, and easy-to-hard generalization. We focus our empirical comparisons on ICM and the bootstrap baselines because they are the methods that address the same task: producing labels from a base model's own predictions, without any external supervision. We would welcome specific pointers to the cross-model consistency methods the reviewer has in mind.

The citation of Shrivastava et al. (W3).

We thank the reviewer for looking into this. We believe there is a misunderstanding: these are two different works by an overlapping group of authors, which is why their author lists differ.

  • Shrivastava et al. (2026), the LessWrong post (January 2026), came first. It breaks down which parts of ICM drive its performance, using ICM's original benchmarks (TruthfulQA, GSM8K-verification, Alpaca) and the same Llama 3.1 models we use. This is where the confident and consistent bootstrap methods we compare against are introduced and evaluated.
  • Canavan et al. (2026) (arXiv:2602.20400, February 2026) is a later follow-up, which the blog post itself announces as upcoming work. It tests elicitation methods on new, harder datasets designed to make them fail. It does not include the confident or consistent bootstrap methods, and it does not evaluate ICM, TruthfulQA, or Alpaca. It uses a single, general bootstrapping method and cites Shrivastava et al. (2026) as its source.

So we cite Shrivastava et al. because it is the work that actually defines our baselines; citing Canavan et al. instead would credit them to the wrong paper. We also cite Canavan et al., in Section 6. The revised version also describes both baselines and their settings in full (Appendix C.3).

Dear Authors Thanks for your reply.

Self-Comparison & Ablations: The ablation study provided by the authors does not include a budget-matched comparison. There are only marginal gains from Phase 2, and it underperforms the baseline without the leakage; LC-UE's advantage on TruthfulQA comes from the gold partition, not the method itself.

Lacking External Baselines: No new peer-reviewed baselines were included. Even though the citation issue is resolved, the informal baseline remains.

Based on that, i remain my score.

Reviewer_JYC4OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes Linear-Cost Unsupervised Elicitation (LC-UE), an efficient alternative to Internal Coherence Maximization (ICM) for extracting labels from pretrained language models without external supervision. To address the quadratic computational cost of ICM's simulated annealing search, LC-UE introduces a two-phase procedure. The first phase generates labels autoregressively, processing groups in descending order of zero-shot confidence. The second phase performs greedy refinement using a low-cost approximation of mutual predictability, with each refinement sweep verified against the exact objective under the configured context limit. Experiments on five benchmarks show that LC-UE achieves comparable or better performance than ICM while substantially reducing the number of model forward passes.

Critical strengths
  1. Substantial computational efficiency improvement. The paper addresses an important practical limitation of ICM by replacing its expensive simulated annealing search with a two-phase procedure. The resulting reduction in forward-pass complexity is substantial, making unsupervised elicitation more computationally accessible.
  2. Competitive performance across multiple benchmarks. LC-UE matches or exceeds ICM on five benchmarks while requiring substantially fewer forward passes. The comparisons with confidence-based and consistency-based bootstrapping methods also provide useful evidence that the proposed approach can achieve a favorable efficiency-performance trade-off.
Critical weaknesses
  1. Limited evaluation of the practical utility of the generated labels. The paper primarily evaluates the generated labels through many-shot prompting. However, an important application of the original ICM framework is to use the elicited labels for downstream model training, including fine-tuning and reward modeling. While many-shot prompting provides useful evidence of label quality, it does not necessarily establish that the all generated labels are equally effective for parameter updates. Consequently, it remains unclear whether LC-UE preserves the practical training utility demonstrated by ICM. A controlled fine-tuning experiment using labels generated by LC-UE and relevant baselines would strengthen the paper's empirical contribution.
  2. Insufficient evidence for the effectiveness of confidence-based ordering in Phase 1. The paper motivates confidence-based ordering as an important component of its efficient initialization strategy. However, Figure 5(a) mainly shows that higher-confidence examples tend to have higher label accuracy and are therefore prioritized earlier in the labeling process. As explicitly noted in the figure caption, the confidence-ordered and randomly ordered curves reach the same endpoint by construction. This experiment does not directly establish that performing the complete autoregressive labeling procedure in confidence order produces better final labels than performing it in random order. A more informative ablation would run Phase 1 independently with confidence-based ordering, random ordering, and possibly reverse-confidence ordering, then compare the resulting label accuracy and downstream performance. Comparing these initialization strategies both before and after Phase 2 would also help clarify the contribution of confidence ordering to the overall method.
Questions for authors

See weakness section.

1 comment

We thank the reviewer for the thoughtful review and the two concrete suggestions. We address both below.

W1. Training utility of the labels.

We agree with the reviewer that fine-tuning is the most direct test of whether the elicited labels are useful for training, and our many-shot evaluation does not establish this on its own. We were unable to run fine-tuning experiments during the rebuttal period. In the revised version, we have scoped our claims accordingly: the abstract and introduction now claim label quality for in-context inference, and fine-tuning is listed as a limitation (Section 6).

We do have three pieces of evidence that the full labeled set, not just the demonstrations, is of high quality:

  1. Accuracy of all training labels. Across every elicited label, the exact set that fine-tuning would use, accuracy is 94.7% on TruthfulQA (with the gold-derived partition; see our response to Reviewer Nzef), 88.9% on GSM8K-verification, and 62.2% agreement with human labels on Alpaca (Table 10).
  2. The TruthfulQA evaluation uses nearly every label. The test-time prompt contains 2,560 of the 2,604 elicited labels, so on TruthfulQA the evaluation depends on almost the entire labeled set, not a curated subset.
  3. Prior work finds the two evaluations agree. Shrivastava et al. (2026) evaluate unsupervised elicitation methods with both many-shot prompting and iterative fine-tuning, on the same benchmarks and base models we use. Their strongest method recovers 83–100% of the gap to gold labels under prompting and 91–99% under fine-tuning, on training sets of the size we use.

W2. Confidence ordering.

We agree with the reviewer that Figure 5a does not answer this question on its own. Its two curves are independent Phase 1 runs on the same 256 TruthfulQA claims, but the caption incorrectly says they end at the same point "by construction." In fact, they end at nearly the same point because both orders produce labels of similar quality. More importantly, a single random seed and training accuracy alone cannot show whether ordering affects the final labels.

Following the reviewer's suggestion, we reran Phase 1 independently in confidence order, random order (three seeds), and reverse confidence order on TruthfulQA, Alpaca, and GSM8K-verification:

DatasetPhase 1 orderingTrain accuracy (after Phase 1)Test accuracy
AlpacaConfidence62.065.2
Random (mean ± sd)62.2 ± 0.464.4 ± 1.3
Reverse confidence62.564.9
GSM8K-verificationConfidence85.471.6
Random (mean ± sd)84.1 ± 1.071.4 ± 0.4
Reverse confidence84.971.6
TruthfulQAConfidence93.787.0
Random (mean ± sd)93.1 ± 0.487.4 ± 0.2
Reverse confidence93.987.6

The order barely matters for the final labels. On all three datasets, test accuracy varies by less than one point across orders, and no order is consistently best. Ordering does change which labels come out early in the pass, but not in a consistent direction: on Alpaca, confidence order produces the most accurate early labels, while on TruthfulQA reverse confidence order does.

We therefore no longer claim that confidence ordering improves the labels. We keep it as a sensible default, motivated by the hypothesis of Shrivastava et al. (2026) that ICM labels easy examples first, and we see the method's robustness to ordering as a practical strength: there is no ordering choice to tune. In the revised version, we have replaced Figure 5a with the TruthfulQA results, added the Alpaca and GSM8K-verification results and the table above to Appendix H, corrected the caption, and revised the related claims in Sections 3.2 and 5.1 (highlighted in blue).

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

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