Model Council Voting

Model Council Voting: Panels of Language Models as Independent Coders

Instructions

A "council" runs the same labeling, scoring, or term-discovery task through several language models independently and reads their (dis)agreement as data. It sits on top of the single-model codebook-and-validation workflow in text-classification — build and validate the codebook there first, then escalate to a council only when one model is not enough. Companion skills: topic-modeling (an independent, non-LLM method for cross-checking what a council finds), llm-calibration-logprobs (per-item confidence from one model's token probabilities, a different signal than cross-model agreement), and methods-reporting (the standards the write-up must meet).

1. When a Council Beats a Single Model

• Use a council when the labeling decision is contested or ambiguous — fuzzy category boundaries, stance or frame coding, constructs where reasonable coders disagree. The disagreement rate is itself a measurable property of the task, not noise to be averaged away.
• Use a council for corpus-driven discovery where the output set is not fixed in advance — e.g., which identity terms a corpus foregrounds. A discovery script of this kind runs a zero-shot extraction prompt over sampled text windows; requiring several model families to independently surface the same term (§4) is what separates a real corpus signal from one model's idiosyncrasy.
• Use a council for robustness reporting when results must survive a skeptical reader. Showing a finding holds across models from different training traditions answers the "would this replicate with a different model?" objection directly.
• A council is overkill when the task is unambiguous and a single validated model already agrees with humans at the level your downstream analysis needs (validate first via text-classification). For high-volume, well-defined coding, N model passes plus the agreement bookkeeping rarely buy anything.
• Decide up front which role the council plays — reliability evidence, robustness check, or discovery filter. It is not a substitute for the out-of-council validation in §7.

2. Assembling a Diverse Panel

• Diversify training families and origins to decorrelate errors. The threat a council guards against is a shared blind spot: models trained on overlapping data or by the same lab tend to make the same mistakes, so they vote together for the wrong reason. One reference term-discovery ensemble deliberately spans four origins — EXAONE-Deep (LG AI Research, Korea), Aya Expanse (Cohere, Canada), Qwen2.5 (Alibaba, China), and Gemma 3 (Google, US) — precisely because "none shares training data or architecture with the others in any direct way, which makes cross-family agreement a conservative test." Four checkpoints from one family is a near-useless council.
• Aim for 3–6 jurors. Below 3 there is no many-rater agreement statistic (§5) and no meaningful k-of-N rule (§4); above ~6 the marginal decorrelation falls off and the bookkeeping grows. Two models is not a council but a pairwise reliability check reported with Cohen's κ, which is how a paired-coder classification study of the same kind uses its model pair. These bounds are house defaults, not a cited optimum; the binding constraint is family diversity, not raw count (§6).
• Prefer open-weight models, pinned to an exact revision and re-runnable locally. Proprietary APIs change underneath you and show high, unpredictable run-to-run variance even at temperature 0 (Barrie, Palmer & Spirling 2025). If a proprietary model is in the council, record its exact dated identifier and treat its votes as the least reproducible (vlm-ocr makes the same point for OCR).
• Pin decoding. Temperature 0 (greedy) is the default so a juror's vote does not wobble between runs. Where you want sampling diversity within a window, that discovery pipeline runs at temperature 0.3 with a fixed window-sampling seed and moves the reproducibility guarantee one level up: "because decoding at non-zero temperature is not bit-for-bit deterministic, reproducibility is enforced at the level of the term set rather than the raw generations."
• Consider an optional reference coder. One stronger or domain-specialized model (or the human-coded gold sample of §7) can serve as the yardstick for per-juror precision and recall — in that study's per-model precision table the Korean-primary EXAONE reaches 56% precision and 100% recall against the nine-term reference, while the English-primary Gemma 3 misses two terms. Keep the reference out of the vote count itself, or you reintroduce a single point of failure.
• Record the exact model tag for every juror — version, quantization, revision, in the form exaone-deep:32b-q4_K_M, aya-expanse:32b, qwen2.5:32b, gemma3:27b. Family-name-only reporting ("we used Qwen and Gemma") is not reproducible.

3. Keeping Votes Independent

• Run each juror in isolation — no model sees another model's output, and there is no multi-round "discussion." Debate or chained prompting collapses the disagreement you are trying to measure and manufactures a consensus that reflects persuasion order, not the corpus.
• Do not pool jurors into one prompt. Asking a single model to "play the role of four experts" yields one model's guess at what four models would say, fully correlated by construction. Independence requires N separate inference runs.
• Hold every shared input constant across jurors. Same prompt, same sampled windows, same seed, same post-processing. That pipeline gives all four models "the same Korean zero-shot prompt, the same adaptive window sampling, and the same wf ≥ 50 absolute floor"; only the model varies, so any disagreement is attributable to the model and not to a moving input.
• For a deliberation design, use $model-committee instead, where GPT-6 Astra and Claude Opus 5 inspect each other's arguments, revise, and cross-rank toward one decision. Debate can improve a single answer, but a debating pair is not a panel of independent raters — do not report debate-derived consensus as if it were independent-coder agreement.

4. Consensus Rules

• State a k-of-N rule before looking at outputs. That discovery study keeps a term only if "at least three of the four models selected it" (3-of-4). Common defaults — 3-of-4, 4-of-6, simple majority — are house conventions, not cited thresholds; higher k buys precision at the cost of recall.
• Prefer absolute floors over distribution-relative thresholds. A per-juror threshold expressed as mean + 2 SD is distorted whenever a few high-frequency items inflate the distribution. That study hit exactly this and switched to an absolute weighted-frequency floor (wf ≥ 50): the mean+2SD rule "is sensitive to high-frequency demonym terms that inflate the distribution in some model runs," whereas "an absolute floor yields more comparable cut-offs across models that differ in extraction volume."
• Add category filters that encode theory, not vote count. A term can win 4-of-4 and still be excluded on principled grounds: that study excludes proper nouns (kingdoms, dynasties, the country itself) "regardless of vote count" because they "function as referential labels rather than contested conceptual constructs" — five terms reach 4/4 consensus and are filtered out this way, visible in its cross-model voting table. Fix which categories are eligible before counting votes, so the filter is a stated rule rather than a post-hoc rescue.
• Run a sensitivity analysis on both dials — the per-juror floor and k. Its weighted-frequency sensitivity table shows the published wf ≥ 50 is "the highest value at which all nine final terms remain while also being the lowest value at which the only additional entrant is a general-register term," and that moving from 3-of-4 to unanimous 4-of-4 drops three substantive terms. Report the band over which the conclusion holds; a set that swings with a small threshold change is not a stable instrument.
• Treat principled abstention as informative, not as a tie. If jurors may return "none / insufficient evidence," count and report the abstention rate per juror rather than silently recoding it as a vote (text-classification makes the same point about NAs as informative missingness).

5. Reading Agreement as Reliability, Not Validity

• Agreement measures reliability — reproducibility of the coding — not validity. A council that agrees perfectly with itself can be perfectly, consistently wrong, and a panel typically agrees with itself more than it agrees with humans. High inter-model agreement is never evidence that the labels are correct; that is what §7 is for.
• Report chance-corrected agreement, not raw percent agreement, which is inflated by the base rate — two coders assigning everything to the majority class agree often by luck. Match the coefficient to the design:

• Interpret κ/α with the Landis & Koch (1977) bands as rough guides, not bright lines: < 0.00 poor, 0.00–0.20 slight, 0.21–0.40 fair, 0.41–0.60 moderate, 0.61–0.80 substantial, 0.81–1.00 almost perfect (that κ = 0.730 is "substantial"). The bands are a convention from one paper — report the raw α/κ value alongside the label.
• Diagnose low agreement before trusting the consensus. Inspect which categories or items drive it: in that same paired-coder study the lowest per-code agreement was civic_commitment at 66.5%, and collapsing two overlapping codes raised overall agreement from 73.0% to 80.9% and κ from 0.634 to 0.730. Low council agreement usually signals a codebook problem (fix it in the text-classification workflow), not a model problem.

6. The Correlated-Errors Caveat

• N jurors carry fewer than N independent votes when their errors are correlated. A majority vote beats the best single classifier only when members err independently; when members are dependent the ensemble can be no better — or worse — than its best member (Kuncheva & Whitaker 2003). Four checkpoints of one model, or four models distilled from a common teacher, tend to be wrong together, so their unanimous vote is closer to one vote than to four. Family diversity (§2) is the lever that raises the effective number of votes toward the nominal N.
• Watch for shared-error signatures. If two jurors miss or hallucinate the same items, treat them as partially redundant — down-weight their joint vote, or report the council with and without one of the pair. A per-model unique-selection analysis, examining which terms each model alone chose, is the diagnostic that surfaces shared vs. idiosyncratic behavior.
• Report the families represented, not just an agreement number. High agreement with low family diversity is weak evidence; high agreement across diverse families is strong. Report the diversity check rather than a single effective-N figure: the general dependence result is well established, but treating it as a precise "effective sample size" calculation for LLM juries goes beyond what can be cleanly cited.

7. Validating Beyond the Panel

• The council must never grade its own work — validate against at least one source outside the council.
• Human-coded gold sample. Hand-code a stratified sample (the text-classification skill specifies 50–100 items, two independent human coders, Cohen's κ or Krippendorff's α for inter-coder reliability) and report each juror's and the consensus's precision/recall/F1 against it. This is the only step that speaks to validity.
• An independent, non-LLM method. Cross-check council output against a method that imposes no LLM prior. The reference study runs BERTopic and LDA over the same corpus and asks whether they independently recover the council's nine terms: BERTopic recovers 9/9, LDA 5/9, with the LDA misses explained by known properties of document-level bag-of-words modeling. The paired-coder study makes the parallel move against an STM ("two independent analytical approaches … converge on the same substantive story"); see topic-modeling for that side of the triangulation.
• Where the council, the human sample, and the independent method diverge, report the divergence — it is usually substantively informative (e.g., LDA misses corpus-wide terms precisely because they are corpus-wide).

8. Reporting and Reproducibility

• Report every juror's exact tag, quantization, revision, decoding parameters, and seed — a complete parameter appendix, not prose.
• Publish the per-item / per-term vote table. The unit-level record of which juror voted which way is the core evidence; the reference study's cross-model voting table gives one row per term with a check/dash per model, the vote tally, and the final status. A reader must be able to see the votes, not just the aggregate.
• Report the consensus rule, the absolute floors, the category filters, and the sensitivity bands (§4), and the agreement statistic with its coefficient, value, Landis–Koch label, and per-category breakdown where relevant (§5).
• State the council's role explicitly — reliability evidence, robustness check, or discovery filter — and report the out-of-council validation (§7). Distinguish discovery from confirmation: if the codebook or term set was revised after seeing council output, report the revision trajectory, since undocumented post-hoc revision is a researcher degree of freedom that can inflate findings (Simmons, Nelson & Simonsohn 2011; Nosek et al. 2018).
• Archive prompts, sampling seeds, the merge/voting code, and the raw per-juror generations so the council can be re-run. For the broader methods-section checklist (APSA/JARS/DA-RT), compose with the methods-reporting skill.

Quality Checks

• Council justified over a single validated model — contested/ambiguous, discovery-driven, or robustness (escalated from text-classification) — and its role stated: reliability evidence, robustness check, or discovery filter
• Panel spans diverse training families/origins rather than multiple checkpoints of one family (EXAONE/Aya/Qwen/Gemma-style spread), with 3–6 jurors
• Open-weight jurors preferred and pinned to exact revisions; exact model tags recorded (version, quantization, revision); any proprietary juror's dated identifier noted and its votes flagged as least reproducible
• Decoding pinned — temperature 0, or a fixed seed with reproducibility enforced at the level of the final set
• Votes cast independently — no cross-talk, no deliberation, no single-prompt role-play; one inference run per juror on identical inputs
• k-of-N rule stated before inspecting outputs; absolute floors used in place of mean+2SD thresholds where jurors differ in output volume; theory-driven category filters applied independent of vote count
• Sensitivity analysis reported on both the per-juror floor and k, with the stability band stated
• Abstentions counted and reported per juror, not recoded as votes
• Chance-corrected agreement reported with the coefficient matched to the design (Cohen for 2; Fleiss for ≥3 nominal; Krippendorff α for ordinal/>2/abstentions) and the Landis–Koch band; read as reliability, not validity
• Disagreement diagnosed per category before the consensus is trusted
• Correlated-error caveat addressed: family diversity documented, shared-error signatures inspected, effective vs. nominal votes acknowledged (Kuncheva & Whitaker 2003)
• Validated beyond the panel — human-coded gold sample (precision/recall/F1) and/or an independent non-LLM method (topic-modeling)
• Per-item/per-term vote table published; model tags, seeds, prompts, voting code, and raw generations archived; discovery vs. confirmation framing and any revision trajectory stated (Simmons et al. 2011; Nosek et al. 2018; compose with methods-reporting)