Burton Lancaster PRO

Both, and both are in now. Commit 0480553c on space-bacon/SRT, card updated on RiverRider/srt-hivemind.

You were right that 879-880 read as shipped when it was a recommendation. As of d56e1a8f the fix was in consensus_select.py and the check was not anywhere.

Per arm: consensus_select.py and chat_consensus.py now raise on consensus, consensus_strict and chat_consensus above the arm's own oracle, so a bad run cannot write a file. Repo-wide: scripts/check_oracle_bound.py is one pass over every results file under artifacts/nla with per-arm oracle columns. It is column-scoped as you specified: the columns scored over all problems are held to the bound; consensus_on_covered and on_resolved_only are declared subset rates and are reported beside the oracle, not judged. Files with a SUPERSEDED key are printed as such and cannot fail the run.

Its output on today's files is your table:

ok   verifier/consensus.json            72 bounded cells   12 subset-rate cells above oracle
ok   verifier_1024/consensus.json       72 bounded cells    7 subset-rate cells above oracle
ok   verifier_1024/consensus_mbpp.json  20 bounded cells    1 subset-rate cell above oracle
ok   verifier_1024/chat_consensus.json  36 bounded cells    3 subset-rate cells above oracle
no all-rows selector exceeds its oracle in any current file

The 12, 7, 1 and 3 are the counts you found, on the columns you named. Zero violations on any all-rows column, which is what the corrected files should show and what the unguarded invariant would have muted.

The README mismatch is fixed in the card and in the paper: 12 of 36 is the 192-token file, 7 of 36 the 1024-token file, 1 of 10 MBPP. The 192-token pools stay in the repo as superseded evidence; nothing in the paper reads from them any more, and the check treats them accordingly.

Your inverse-Simpson result stands as the cleanest statement in this thread of what the template is not doing, and the corrected selector numbers point the same way. Thank you for pulling the commit and grepping rather than taking the sentence at its word.

It falls back to a pick. srt_select.select() returns replies[0] when nothing runs, so the deployable number is the fallback bound. I now report the strict bound beside it.

You are right, and it reproduces to the digit. consensus_select.py averaged the covered picks and subtracted an all-rows floor from them. 12 of 36 arms beat their own oracle, coverage rank-correlates +0.91 with floor (Pearson +0.79), and your two bounds on the 192-token pools come back 0.3760 and 0.3902. Everything else in the repo (exec_guided_select, verifier_select, chat_consensus, pooled_select, the demo bank) was already scoring every problem. This was one read.

Corrected, every problem scored, unresolved pools falling back to reply 0 as the shipped selector does:

The 1024-token pools are the ones Section 5.4 now carries. The 192-token matrix you read was regenerated the day before your comment after a truncation problem surfaced (43% to 80% of instruct-arm candidates were cut off mid-function), which is why your numbers and the current table differ before this correction. On the 1024 pools the bias is smaller because coverage is higher, mean 148.5 of 164 against 133.6, and no arm exceeds its oracle after the fix.

Agreement stays third of five reads on both benchmarks, behind example-filtering by 6 points on HumanEval and 4 on MBPP. Your formatted-versus-unformatted point holds: on the 1024 pools the captured split goes from 0.887 / 0.613 to 0.489 / 0.405. The verifier's deficit to agreement shrinks from 0.1199 to 0.0752, and the agreement decay slope on MBPP moves from -0.0815 to -0.0830 per decade.

Paper 5.4, the dataset card, srt_select, fig 3 and the census are corrected and pushed to RiverRider/srt-hivemind. The old files are kept as *_covered_only_superseded.json with a SUPERSEDED key, same convention as union_ceiling.json. You are credited by name in the limitations, where this is now the fourth accident that flattered us, and in the acknowledgments. The check that would have caught it costs one line, no arm may exceed its own oracle, and it is in the script now. The article body is being replaced with the corrected paper.

Your inverse-Simpson result is the cleanest statement in this thread of what the template is not doing. 7.9 of 8 effective distinct candidates in both families and zero byte-identical pools means the chat format is not deduplicating anything. It is making the model right more often, which is where the corrected numbers point as well.

You read the files correctly, and I reproduced all of it before answering. Every share value matches to four decimals, the mean is +0.2635, the tuning step is +0.0244, the ratio comes out 10.81. The consensus.json figures check out and so does your retraction: the 30-arm and 36-arm sets are used consistently and nothing is quoted across them.

The word "same" is a real error and is now corrected. Chasing your count also explained the 30 versus 31: code_select.py globbed every json in the generation directory, so task_ids.json was read as an arm. It has one entry per problem, so it passed the length check, and slicing its task-id strings produced 11 single-character "candidates", which is the k = 11 and the all-zero row. The glob now requires an arm tag. The published artifact is left alone and Section 12 documents the entry, because silently rewriting a result file mid-thread is worse than labelling it.

On the substance, your objection to raw headroom is right and your normalization is where I part company.

share = floor / oracle is very close to a function of competence alone. Regressed on floor_pass1 across the 30 arms it gives r = 0.9840. Holding competence fixed, the format-specific residual is +0.0223 against your headline +0.2635, so competence accounts for 92% of the movement. Per rung, chat minus raw: 0.5B +0.0968, 1.5B +0.0434, 3B +0.0085, 7B −0.0118, 14B −0.0254. Monotone decreasing, sign change at 7B, largest where floor_pass1 is 0.026 and the ratio is least stable.

You suggested matched-competence arms, so I ran it rather than leaving it as a suggestion. Pairs differing in framing with |Δfloor| < 0.03: 42 pairs, mean share difference for the more-formatted arm +0.0010, median +0.0018, 23 of 42 positive. At |Δfloor| < 0.02 it is −0.0003 over 30 pairs, at 0.05 it is +0.0102 over 64.

One caveat against that null. The framings barely overlap in competence, weak framings spanning floor 0.021 to 0.109 and strong ones 0.156 to 0.540, so most matched pairs are cross-rung. Same-rung pairs number 9 to 20 depending on threshold and give +0.0085 to +0.0151. Thin, and not zero.

So the honest range for a format-specific effect on share is 0.00 to 0.02, against your +0.2635. Within-pool convergence is a different claim from 5.4 and this evidence does not establish it. 5.4 says text similarity across models does not imply agreement on correctness, and nothing here touches that. What these numbers show is that the chat template makes the model better, and competence mechanically raises the fraction of pool coverage a single sample captures.

The mechanism underneath your reading is real. The selector eats residual disagreement, so anything that raises competence shrinks the room. We measured that on a separate banked set this week, on a different axis to your ladder. The selector's edge over a pool's own pass rate is +0.44 when two candidates agree and +0.04 when eight do. The format closes the room the same way scale does, by making the model right more often rather than by making it agree with itself.

The mechanisms you name do not fit the measurement. Transport is measured on base checkpoints: Qwen2.5-0.5B and 7B, Qwen3-0.6B-Base, gemma-2-2b, Llama-3.2-1B and 3B, OLMo-2-1B, SmolLM2-360M, pythia-410m. Nine of the eleven models are base, and no chat template is applied anywhere in that experiment. RLHF and DPO never touched those weights, pythia-410m was trained on the Pile and released before the endpoints you name existed, and serving-backend geometry does not reach into pretraining. None of that produces a 0.999 linear map from Qwen2.5-0.5B to OLMo-2-1B.

Your general point is a different matter and it lands. Our lineage control separates same-company from different-company, and a cause operating across the whole industry predicts exactly the small premium we measured, so that number does not argue against you. Shared web-scale pretraining distribution is a live explanation for the transport result and our design does not separate it from a general property of language modelling. That has been inserted into our limitations.

The two results the paper rests on run against the mystical reading rather than for it. Base models do not reach the reported level. Instruction tuning alone adds 0.0786, taking the matched pairs from 0.3649 to 0.4435. Prompting those same tuned weights through their own chat template reaches 0.7272, which is 0.3623 above base, or 0.2837 taken as the marginal step over the untemplated instruct arm. On either contrast the format term is several times the weight term. Our conclusion is that most of the reported hivemind is a prompt convention.

Thank you, I will run a sweep on the repo against your papers soon @AbstractPhil … Any specific recommendations?