acceptodds
Under review as a conference paper at ICLR 2027

Sources Count, Copies Win: A Gap in LLM Evidence Aggregation

Abstract

Large language model (LLM) agents search documents and exchange messages to gather evidence, yet duplicated study reports and recirculated messages can turn one observation into apparent consensus. Human experiments show that repetition can increase perceived truth even when people demonstrate knowledge of the correct facts in a separate test. We investigate whether LLM decisions remain vulnerable when shared provenance is explicit and source-counting ability is assessed separately. Our Explicit Evidence Groups task varies redundant records while holding independent support and the correct answer fixed. Across seven different LLMs, increasing a minority source from one to sixteen records reduces decision accuracy by 17.2–40.6 percentage points, even without repeated answer labels. Linear probes recover source-count and repetition information before a decision, and separate numerical reports often preserve the correct source ordering despite counting errors. Head selection and causal ablations reveal partially distinct attention-head contributions to source reporting and direct decisions. Reporting source counts before choosing improves decisions under repetition when the task remains within the models' counting capacity. Our findings show that explicit provenance alone cannot ensure reliable evidence aggregation: information about independent sources can be available without reliably constraining decisions. For scientific synthesis and multi-agent deliberation, reliability requires preserving the distinction between evidence that gains independent support and evidence that merely gains circulation.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Large Language Models, Evidence Provenance, Evidence Aggregation, Transcript Multiplicity

Reviews

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1234this paper, Bottom 10%
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.
Reviewer_9uWCOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper studies whether LLMs confuse repeated records with independent evidential support even when provenance is explicitly supplied. It introduces the Explicit Evidence Groups task, in which each source denotes one independent observation, multiple records from the same source are declared redundant, and the correct answer is determined by the number of independent sources. The main experiment fixes a one versus two source minority and majority relation while increasing the minority source's record count from d=1d=1 to d=16d=16.

Across seven selected open weight models, the paper reports a 17.2 to 40.6 percentage point loss in decision accuracy in the label free setting. It also evaluates repeated answer labels, neutral context extension, balanced repetition, and a genuine increase in independent sources. The paper then separates information availability from information use through linear probes of source and occurrence counts, explicit numerical reports, activation times gradient head selection, and final query head ablations. Finally, it tests a count first prompt that requires the model to report source counts before deciding.

The behavioral result is clear within the controlled task: repeated records can move choices toward a source minority, while all seven models respond to a genuine increase in independent support. Source and repetition information is often decodable or reportable, but this does not guarantee a correct direct decision. Count first prompting improves all models at low repetition, but becomes mixed at high repetition as count reporting deteriorates.

Critical strengths
  1. The primary behavioral diagnostic is controlled and interpretable. The source majority and correct answer remain fixed while repetition dose changes, both label assignments are evaluated, and the label free condition removes repeated answer letters from added records. The genuine source increase control is particularly important because it shows that the evaluated models are not simply insensitive to source structure. Five of seven models also show positive paired intervals against both neutral extension and balanced repetition controls.

  2. The paper provides a substantial and transparent decomposition of the failure. The probe experiment uses disjoint source identifier pools across family level train, validation, and test splits, with length only and shuffled label controls. The report experiments reveal a meaningful difference between exact count accuracy and preservation of source ordering. The head analysis uses frozen discovery selections, held out surfaces, matched random groups, stratified bootstrap intervals, and multiple comparison correction. The count first experiment is also appropriately reported as dose dependent rather than as a universal solution.

Critical weaknesses
  1. The novelty relative to existing work is limited. The related work section does cite the closest precedents, but the distinctions it draws from them are narrow. Schuster et al. (2026), "Whose Facts Win? LLM Source Preferences under Knowledge Conflicts" (ACL 2026, arXiv:2601.03746), already show that repeating information from a less credible source reverses the source preferences of 13 open weight LLMs, and the paper's own related work attributes to it both the same source repetition versus additional source attribution comparison and a separate validation of source recognition and table reading; the present paper's stated difference is only that its equal weight rule fixes the correct choice. GroupQA (Naphade, 2026, Findings of ACL 2026) already reports that paraphrasing an argument is more persuasive than providing distinct independent support, and, according to the paper's own related work, also checks conflict detection and document level stance attribution. CAMA (Lin et al., 2026, arXiv:2608.19701) already formulates correlated memories as a false majority and estimates the effective number of independent evidence sources; the present paper's stated difference is that the correct groups are supplied rather than inferred. The general distinction between a correct intermediate computation and the computation that controls the output is likewise attributed in the paper's own related work to Zhou et al. (2026) on negation processing (arXiv:2605.03052). The present paper's strongest remaining novelty is therefore the particular combination of an explicit source count task, count and occurrence probes, and cross task head ablations, rather than the discovery of the behavioral failure or the general availability versus use distinction.

  2. The evidence does not yet establish the proposed mechanistic explanation or broad generality. Count and Direct use different prompts and different output spaces, numerical tokens versus evidence group letters, while ablation is applied only at the final query position. The resulting interactions establish different relative final query contributions, but not a distinct counting circuit or failure to recruit that circuit during Direct. The paper also does not test whether the selected heads mediate count first improvements, which it correctly acknowledges. Separately, model inclusion depended on observed baseline accuracy, repetition sensitivity, and reporting behavior; the reported 64 surface estimates include 16 discovery surfaces; four of seven models are from the Qwen family; and the surfaces vary identifiers, order, and wording within shared templates rather than constituting independent tasks. Neutral and balanced controls also do not exactly match token length or insertion position. These choices support a controlled within model phenomenon, but not a prevalence claim or strong generalization to open ended evidence synthesis.

Questions for authors
  1. Beyond supplying the source groups explicitly, how do the authors distinguish the central contribution from Schuster et al. (ACL 2026, arXiv:2601.03746) and CAMA (arXiv:2608.19701)? Schuster et al. already show that repetition reverses source preferences even for less credible sources, and the paper's own related work credits them with validating source recognition separately from the decision; CAMA already estimates the effective number of independent evidence sources. Please state precisely which empirical or mechanistic conclusion remains unique after accounting for these works, and in particular what the equal weight source majority rule establishes that explicit source attribution under a credibility rule does not.

  2. Can the authors report the primary dose effects in Table 3 using only the 48 surfaces withheld during model selection, excluding the 16 discovery surfaces? Please also state whether the 32 surfaces used for the context controls in Table 4 overlap with the discovery surfaces, and whether the 104 family count grid and the 192 family count first grid played any role in model selection. Please also provide the complete candidate model inclusion and exclusion process. Because repetition sensitivity was one selection criterion, a fully held out estimate is important for judging the robustness and magnitude of the effect.

  3. Is there direct evidence that count selected heads are recruited by the count first prompt or causally mediate its gains? A matched output formulation, intervention transfer test, or mediation analysis would help distinguish source counting from differences caused by producing numerical rather than letter outputs. Without such evidence, should the claim be narrowed from a mechanism explaining the behavioral gap to task selective final query contributions?

Reviewer_VHesOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper provides an empirical study of how the repeated records from a single source will affect LLMs' decisions in the case that the decision rule is majority votes over different independent source. This study claims that even when the LLMs' hidden layers contains the information about source counts, LLMs' accuracy may still decrease as the repeating records increase from single source via a controlled diagnostic task and an analysis linking behavioral repetition bias with internal representations and causal attention-head analysis by dividing the heads into counting heads and direct heads. It also claims that they show that explicitly invoking source counting can improve evidence-based decisions without additional training within the models’ counting capacity.

Critical strengths
  1. They provide a clear control design for their study target including holding the total number of independent source fixed while changing the number of records and the reverse. The experiment is designed as a label-free task, which can isolate the repetition bias from the answer letter frequency. They also control the label preference bias by swapping the evidence group label. It controlled the bias may come from the context length.
Critical weaknesses

This study supports its claims in the following way.

First, they state that the source and occurrence counting information is in the final hidden state in figure 4. Then, they report that those decisions can rely on different attention-heads in figure 5. Finally, they claim count-first can improve the decision performance in table 1.

However, in figure 4, as the number of source increases, the accuracy of linear probes decreases aligned with the model report accuracy. This result shows that the information itself becomes unclear as the number of source increases, which may not be enough to support that the model does not fully use the counting information. In figure 5, the separation is not that clear for most models. Only 9B, 27B, and Idefics3 show a clear double dissociation. In table 1, the trend is unclear for most of the models. Especially for Idefics3-8B and Granite-3.3-8B, the gain even becomes negative as the number of repetition increases.

Questions for authors
  1. Could you test whether count-first reduces the accuracy decline as repetition increases using ways like GLMM? You claim that count-first improves decisions under repetition, but the table 1 only shows that count-first generally improves the model performance for some of the models, while the trend of improvement as repetition increases is not tested.

  2. Could you explain the reason that there is a positive gap between Correct order in table 8 and the count-first accuracy in table 1 at d=16? Since the gaps of Qwen3-30B-A3B and Nemotron-4B are more than 20pp, this suggests that the final choice is not consistent with its reported count. How often does the final answer match the reported count, and how often are the reported counts ties?

  3. Could you explain the reason that the separation is not that clear for most models in figure 5? For example the direct head of Qwen3-30B-A3B even have a negative effect on held-out direct setting. And only 9B, 27B, and Idefics3 show a clear double dissociation.

  4. Could you explain how figure 4 can support the claim that the model does not fully use the counting information, as the accuracy of linear probes and the model report accuracy decrease together as sources per option increase?

Reviewer_WAd3OpenReview ↗
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Confidence
3
Informativeness
1
Presentation
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Soundness
1
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Paper summary

The paper studies whether LLMs aggregate evidence by independent sources or by number of records. In a synthetic task where source identities and redundancy are explicit, repeating a minority source’s records from 1 to 16 reduces decision accuracy by 17.2 - 40.6 points across seven open models of 30B parameters or fewer. Linear probes and attention-head ablations suggest that source-count information is present but used differently when counting and when choosing. The paper proposes count-first prompting (reporting source counts before choosing) as a training-free fix, which helps at low repetition but not consistently at high repetition.

Critical strengths

The controlled task design isolates repetition from added context. This makes the behavioural effect credible, but it does not offset the limited novelty and intervention.

Critical weaknesses

Weakness 1: The main finding is largely known, and the mechanistic analysis is inconclusive.

The core result is that repeating one source’s records shifts model choices even when the repeats are marked as redundant. Prior work already establishes closely related effects:

  • Schuster et al. (2026) show that source preferences “can be reversed by simply repeating information” from a less credible source.
  • Naphade (2026) finds that paraphrasing an argument “can be more persuasive than providing distinct independent support”.
  • Lin et al. (2026) identify correlated evidence being “repeatedly counted” as a “false majority”.

The evidence base is also narrow. All items come from one template (Appendix A: “not independently authored tasks”). The seven models were selected partly for “repetition sensitivity” (Appendix B). The key evidence that models know the counts yet choose wrongly rests largely on one model: Qwen3.8-27B reports exact counts in 46 of 48 cases, while the other six manage 0 - 10 (Table 7).

The mechanistic analysis does not close this gap:

  • The probes show that count information can be decoded, not that the model uses it.
  • The head differences may reflect number vs. letter outputs, which the authors themselves say “limit circuit interpretations” (Appendix E).
  • The link between the heads and the count-first gains is untested.

What remains is a variant of a known effect, shown on template-generated items with partly behaviour-selected models. That is not enough for a new contribution.

Weakness 2: The proposed intervention is a model-specific reasoning prompt without proper baselines.

Count-first prompting asks the model to report source counts before choosing. This is a standard decomposition prompt, closely related to chain-of-thought and plan-and-solve. It is compared only against answering directly, with no chain-of-thought baseline and no comparison with the repetition mitigation of Schuster et al. (2026). So the gains cannot be credited to counting rather than to reasoning before answering.

The prompt is also not one fixed method. Appendix G gives Idefics3-8B an extra instruction that spells out the comparison rule, and Nemotron-4B a different, set-based instruction. The intervention was adjusted for individual models.

Even so, the gains are not robust. At 16 repeats, Granite’s accuracy falls significantly , and two other models show no change (Table 8). Exact count reports fall to 8 - 54%, which limits the method in exactly the setting it targets.

Count-first prompting is the paper’s only practical contribution. As evaluated, its benefit cannot be told apart from generic step-by-step prompting, and it depends on model-specific prompt wording.

Questions for authors
  1. Why do Idefics3-8B and Nemotron-4B receive different count-first instructions (Appendix G)? How do they perform with the default instruction?

  2. Which models were evaluated and excluded during selection, and on what grounds?

  3. How does count-first compare with a plain chain-of-thought prompt and the related work?

  4. Does ablating the count-selected heads remove the count-first gains?

  5. Do you test whether the effect persists in larger models and in settings where source dependencies must be inferred rather than given.

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

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