Posttraining and Adaptation

Change small-model behavior through LoRA, DPO, distillation, GRPO, DAgger, and other update mechanisms.

What we have learned

Seed Experiments

Key Result

qwen35_4b_meta_induction (general arm) (claim C45): GENERAL induction-via-reasoning IS installable -- a general hypothesize-and-verify CoT trained on families {a=1,3,9} transfers to held-out a=7 (0.905, as high as in-family). The fixed 4B can be taught general induction, but only as a serial reasoning procedure (C44: forward-pass 0.01). Teach the general strategy across diverse cases + deploy with chain-of-thought.
qwen35_4b_meta_induction (reasoning arm) (claim C44): the forward-pass induction wall is a SERIAL-COMPUTE limit, not a knowledge limit -- reasoning-SFT induces held-out shifts perfectly via generation (1.00) but at chance in one forward pass (0.01); the CoT is 100% load-bearing. Give the model serial tokens and induction works; it cannot be compressed into a forward pass.
qwen35_4b_meta_induction (claim C43): can SFT install the induction skill? PARTIALLY -- shift induction 0.087 (chance) -> 0.40 (data-limited) but plateaus below the execute ceiling (0.72), is shift-specific (OOF affine 0.30), and answer-only SFT catastrophically forgets execution (0.72 -> 0.09). The wall is neither a hard bound nor cleanly liftable; trained to induce, the model learns a specific procedure, not the general skill.
qwen35_4b_learn_from_failures (claim C29): preference training on the model's OWN failures does NOT close the coverage->deployable gap -- DPO collapses generation (greedy@1 & coverage crash; pre-DPO 2AFC=0.81 verifier but preference-optimizing it destroys the model). The gap closes with MORE SFT: SFT_2x triples greedy@1 (0.037->0.113). Extends prior MBPP DPO work to the controlled depth-3 substrate. Limits: DPO not heavily constrained, single seed.
qwen35_4b_bank_the_thoughts (claim C28): banking correct decomposition PLANS beats banking ANSWERS on deployable depth-3 -- three fresh QLoRA on matched data (A=prompt->code, T=prompt->plan->code, T_corrupt=mismatched plan); T coverage@16 0.325 vs A 0.200; content-causal (T_corrupt collapses to 0.113, below A); test-time channel (T no-think 0.013). Resolves C26/C27 (thinking helps once the reasoning is banked). Limits: synthetic plans (Phase 2 = model's own thoughts), step-1-think eval incomplete, single seed.
qwen35_4b_decompose_compose_frontier (claim C12): banking search+interpreter-harvested solutions (QLoRA-SFT, no teacher) that the model could NOT monolithically sample EXTENDS its frontier into the weights — monolithic held-out pass@5 0.125→0.237 (+0.112, ~2.6 SE), depth-3 pass@5 4×. This breaks M4's coverage bound: self-training on data from OUTSIDE the sampling support (harvested by tool-augmented search) pulls it into the distribution. Frontier extension without a teacher.
qwen35_4b_neurosymbolic_repl_substrate (claim C11): the corpus's first self-training WIN. QLoRA-SFT on the 4B's OWN 189 execution-verified solutions (no teacher) improved held-out fresh single-shot on a contamination-free substrate: think-greedy@1 0.224→0.319 (+0.095, ~2.2 SE, N=210), pass@5 up (NO diversity collapse), two seeds. This works where the corpus's MBPP self-improvement regressed (qwen35_4b_verifier_guided_self_improvement) — implicating contamination/substrate, not the method. (Test-time execution-feedback self-correction, by contrast, did NOT beat matched-compute sampling — same experiment, M2.)
qwen35_4b_answer_potential_trace_sft (claim C51): a dense reference-answer score did not earn the right to become an SFT curriculum. It carried modest within-task signal and passed shuffled/foreign/format controls, but missed its AUROC and practical top-choice uplift gates. Almost every thought was cap-bound and only 13.2% of forced-close answers parsed. The preregistered guard stopped before N=128, selection, or training, so this is a scorer negative—not an SFT negative.
qwen35_4b_balanced_core_answer_potential_sft removes the 512-token cap and banks six deterministic selections, but remains pre-training. Equal 720-row arms hide a 34,446,994-forward-token two-epoch matrix because selected thoughts reach 14,325 tokens. They also hide unequal support: success-RFT has only 97 unique traces from 58 tasks and repeats them seven or eight times. This is a resource/support feasibility result, not evidence that potential-selected SFT works.
qwen35_4b_think_ftpo_round2 (claim C52): selecting only low-entropy, non-degenerate-varentropy confident wrong turns did not rescue single-token preference training. Positive-only chosen-token uplift was safer than conventional demotion and true labels separated from shuffled labels on the parent gym (+6.25pp) and fresh repository agent (+13.89pp, CI touching zero), but every LoRA arm failed the exact-logit locality ceiling. Held-out coding remained below base (39/72 vs 43/72), so the registered result is a low-dose capability null, not a new adaptation recipe.
qwen35_4b_specialist_policy_integration: the first same-origin specialist/MOPD test stopped before best-of-8 or any specialist update. Its full paired baseline put the only tools family at 0.994, making the mandatory S0 + 0.10 target 1.094 under a hard score cap of 1.0. This is a posttraining-design feasibility negative, not evidence for or against MOPD; every mandatory arm now needs a ceiling/headroom check before production.
qwen35_4b_pareto_policy_integration: the corrected successor removed the fixed effect-size floor and completed two paired qualification blocks. The assumed quick teacher was negative in both (-0.00693, -0.03789; pooled -0.02241), while the deep teacher had a credible +0.04563 capability advantage but failed six retention cells. Every protocol check passed. The stop occurred before teacher audit or MOPD, establishing a teacher-transport prerequisite rather than a distillation negative.
qwen35_4b_same_prefix_advantage_routing: the clean state-level successor used 384 fresh soup states and disjoint four-branch selection/audit continuations. Deep passed both student and alternate contrasts in both blocks (student macros +0.1216, +0.0655; pooled one-sided LCB +0.0657), and the combined router passed. Quick did not: its soup-relative audit macro changed from +0.2009 to -0.0253 even though the pooled LCB was positive. The preregistered stop prevented MOPD. Diagnostics localize the issue to winner-conditioned labels: only 6/26 block-1 quick routes remained strict audit winners, and +0.10/+0.25 observed margins remained negative. This is a two-teacher estimator negative, not an MOPD negative.

Current Read

Adaptation is useful only when the target behavior is well specified and controls expose whether training changed the intended mechanism — AND on a substrate where a gain is even measurable. C11 shows honest self-training (own verified solutions, no teacher) banks capability into single-shot on a CONTAMINATION-FREE substrate, reversing the corpus's earlier "self-training loses to sample-more" reads that were likely confounded by contaminated/saturated benchmarks. Priority: scale the self-training loop (expert iteration), test cross-substrate transfer, and re-run the failed MBPP self-improvement with contamination controls.

C51 sharpens the curation prerequisite: before comparing posttraining arms, prove that the proposed dense label selects deployably better traces at useful effect size. A teacher-forced answer state after an injected close is not automatically a valid SFT target source, even when corruption controls say the score notices relevant content.

The uncapped continuation adds dose and support prerequisites. Count-matched long-trace datasets can be grossly compute-mismatched in practice, while an outcome-filtered control can collapse to a small, easy-task support and become repetition training. Forecast exact forward tokens and audit task/cell support before freezing a multi-arm adaptation matrix; preserve a smaller run as a separately scoped experiment.

C52 adds a separate intervention prerequisite: a label can contain real directional information while its shared-parameter update is too non-local to transfer. Confident-outlier geometry and entropy/varentropy routing do not replace an exact-logit locality gate. Positive-only pressure is preferable to pairwise demotion, but do not scale it until the update clears ≤0.10 median non-target drift on independent contexts.

The specialist stop adds a still earlier prerequisite: prove that each mandatory arm can mathematically clear its frozen gain rule. Aggregate endpoint headroom can coexist with a saturated arm, so average calibration cannot license a multi-arm adaptation run by itself.

The corrected successor adds the next prerequisite: even a source policy that wins an external aggregate tier may not be locally better on the student's clean rollout distribution. Distillation needs replicated same-prefix teacher advantage, not a checkpoint label. The most informative continuation is a fresh outcome-routed pilot that estimates both teachers' verified continuation values before any update; reusing coarse quick/deep routing would repeat the measured mismatch.

That continuation now resolves the next boundary. Same-prefix verification did find a replicated deep advantage, but four-branch three-way argmax did not produce a stable quick route. Absolute policy estimates correlated 0.79-- 0.86 across halves; conditioning on the largest noisy estimate caused the failure. The clean update test was therefore fresh deep-only routed MOPD from the joint soup. Two-teacher composition remained downstream of cross-fitted direct advantage prediction and a third untouched block, not a larger fixed effect-size threshold.

That deep-only successor passed fresh qualification, exact-logit locality, three four-round optimizer seeds, all three matched trained controls, and the 25%/50%/75% parameter-soup construction gates. The independently replayed controls receipt is 103ef4cc0b24d7c10666b6f0adfcd4dfae4720415c7fbbc76b681ab79162640b. The same-backend sealed comparison then rejected installation: primary seed 42 was −0.006845 joint versus deep, −0.003706 versus soup75, and −0.169239 versus soup best-of-eight; seeds 43/44 also trailed deep. Retention and transfer passed. Correct-teacher pressure did beat wrong-teacher (+0.005312, one-sided LCB +0.000099) and non-advantage MOPD (+0.005619, LCB +0.000582), so the route signal is causal enough to move the checkpoint but insufficient to cross the source frontier.

This elevates the measured NF4/bf16 parity failure from caution to design prerequisite: mean NF4 objective gain was +0.02191, explicit bf16 gain was −0.000224, and correlation was −0.152. Before any larger or two-teacher MOPD run, directly train a bf16 micro-update and require its deployed checkpoint to beat the source, interpolation, and matched-compute sampling. Cross-fitted advantages, adaptive allocation, and a third block remain necessary for later two-teacher work, but they cannot rescue a non-deploying update operator.

Scorecard

Program: charter
Current read: adaptation can reshape behavior, but the beyond-C53 line now exposes seven launch boundaries: use deployable outcome-valid targets; preserve neighboring behavior; make every absolute gate feasible; verify teachers on the student's same-prefix distribution; estimate conditional teacher advantage without winner's curse; preserve verifier-conditioned recovery; and prove that the training update survives the deployed merge. Deep-only routed MOPD passed route, locality, retention, transfer, and directional teacher/control tests, yet all three seeds trailed deep and primary lost to interpolation and sample-more. The NF4 objective gain reversed after bf16 merge.
Best next experiment: direct-bf16 deployment-parity microtraining with a hard merged-checkpoint gate against deep, interpolation, and matched-compute sampling. Only after it passes should two-teacher work add cross-fitted direct advantages, adaptive allocation (including zero quick), and a third untouched block.
Strong anchors: qwen35_4b_gauntlet_breadth_round1, qwen35_4b_gauntlet_frontier, qwen35_4b_bank_the_thoughts, qwen35_4b_answer_potential_trace_sft, qwen35_4b_think_ftpo_round2, qwen35_4b_specialist_policy_integration, qwen35_4b_pareto_policy_integration, qwen35_4b_same_prefix_advantage_routing, qwen35_4b_deep_advantage_mopd, qwen35_4b_repo_search_compress_bank.
Avoid repeating: unauditable adapters, hidden-label wins without frozen alternatives, infeasible mandatory arms, coarse teacher labels, four-branch statewise argmax as a two-teacher labeler, posthoc route margins, non-local sparse steering, or success-only banks that erase recovery.
Evidence that advances the program: a trained behavior beats strong frozen/tool baselines without hidden-label leakage.

Charter

Show charter.md

Purpose

Study how small-model behavior changes under lightweight updates: LoRA, QLoRA, DPO, distillation, DAgger, GRPO, preference objectives, and process supervision.

Why This Is A Program

The repo should support many adaptation mechanisms, not treat any one method as default. The central question is which update target changes the model in the desired direction without destroying generality or safety.

Progress Signals

Updates beat frozen baselines and non-mechanistic controls.
Gains transfer beyond training-like tasks.
Training artifacts are reproducible without checking adapter weights into git.
The update objective explains the behavioral change.

Boundaries

This program owns model updates. Candidate generation, selection, or tool control can be downstream beneficiaries.

Backlog

Show backlog.md

Next Experiments

Active model-free intake: qwen35_4b_counterfactual_plan_reflection_transfer isolates the workspace paper's counterfactual-reflection training claim from C28's direct plan-and-answer SFT. The correct and within-family shuffled arms receive loss only on a hypothetical plan response after a shared READY state; neither receives the query answer as a target. CPU construction and adversarial design/implementation review must finish before any model event. Require a replicated held-out action-branch win over shuffled reflection and same-backend frozen sample-more before opening conditional J readout or causal ablation.
Completed cross-program qualification negative: qwen35_4b_pareto_policy_integration replaced the arbitrary absolute bar with replicated paired delta > 0, then found that C54's labels did not transport to the clean distillation proxy. blend was negative on quick in both blocks; apex was positive on deep but failed retention. No MOPD update ran.
Completed route-qualification negative: qwen35_4b_same_prefix_advantage_routing scored 384 fresh soup states with disjoint selection/audit branches. Deep independently passed, and the combined router passed, but quick reversed from +0.2009 to -0.0253 versus the soup across blocks. Four-branch statewise argmax is stopped as a two-teacher labeler; the later deep-only successor tested MOPD and is recorded below.
Completed capability negative: deep-only verifier-backed MOPD from the 40/60 soup passed route qualification and locality but trailed deep, soup75, and sample-more on sealed confirmation. Correct-teacher and advantage-state controls were directionally positive, so preserve the route signal; do not repeat the NF4 update operator at larger scale.
Highest-value new experiment: direct-bf16 deployment-parity microtraining on fresh procedural states. Require the merged causal update to beat deep, ordinary interpolation, and matched-compute sampling before opening a full campaign. Include the same route/non-route/wrong-teacher controls so update survival, not only target quality, is identified.
A later two-teacher successor must estimate each direct teacher - student advantage with cross-fitting and uncertainty-aware branch allocation, freeze the predictor, and confirm both teachers on a third untouched block, after the direct-bf16 operator gate passes. Permit zero allocation to a teacher without independent conditional value. Do not retry statewise three-way argmax or repair it with a posthoc fixed margin.
Stopped cross-program test: qwen35_4b_specialist_policy_integration reached a design-feasibility negative before any specialist or integration update. Its sole tools core scored 0.994 at baseline, so the mandatory +0.10 gain required 1.094 on a score capped at 1.0. A new run must use a harder, independently calibrated tools/provenance core and prove every arm's theoretical headroom before best-of-k or training; do not amend this result.
Treat any C51 follow-up as a new close/commit-scoring experiment, not a larger rejection-sampling run; require autonomous termination and parse gates before training.
Treat any C52 follow-up as a locality experiment first: compare lower-dose positive-only uplift with a context-gated intervention, and stop before downstream training/evaluation if exact-logit non-target drift exceeds 0.10.
Compare DPO, SFT, process distillation, and DAgger on one shared candidate/evidence substrate.
Add adapter-free reproducibility manifests for every trained run.
Measure catastrophic narrowing: does an update improve one substrate while hurting direct baselines?
Train on hard negatives and evaluate whether coverage or selection improves.
Distill process labels only when labels are deployable or clearly marked oracle-only.
C45 follow-up: compositional-grammar reasoning-SFT. Teach a serial hypothesize-and-verify search over condition x action rules, with mixed execute examples to prevent forgetting. Evaluate held-out combinations, held-out productions, and held-out composition-depth separately; require execute-ceiling gates, token-budget/truncation checks, and branch-coverage/value-fill sufficiency checks before interpreting induction failures.

Required Controls

Frozen model.
Shuffled labels or shuffled traces.
Same-token-budget sampling.
Held-out task and family evaluation.

Stop Conditions

Do not retain trained adapters in git. Do not claim a posttraining method works if it beats only a weak baseline and fails frozen or shuffled controls.

Do not spend SFT compute on a trace score that has not cleared a preregistered within-task outcome gate and practical top-selection margin. C51 is stopped before training under its current answer-only potential event.

Do not spend posttraining compute on a mandatory arm whose frozen absolute gain criterion exceeds its score ceiling. Endpoint-average headroom does not establish per-arm feasibility.

Do not distill from a teacher merely because it won an external aggregate instrument. Require positive same-prefix continuation advantage on the actual training-state distribution, replicated on a disjoint block.

Experiments 103

2026-07-19 Qwen35 4B Agentic RLVR Feasibility
Yes to the machinery: with three fixes (force eager mode so the hybrid architecture doesn't hang, load the model in bf16 not fp32, and split GPU memory 55% to the inference engine with sleep-mode) the loop CLOSES - a mov
2026-07-18 → Qwen35 4B WHY-Think Scale
This phase built and proved the machinery; the GPU training sweep has not run yet. The generator now emits, for every example, a real hidden reasoning trace generated mechanically from the program's shape - parse the spe
2026-07-18 → Qwen35 4B WHY Scale Ladder
This phase built and proved the machinery; the GPU training sweep has not run yet. The core blocker was that the original WHY generator saturated fast (about 75 distinct reasons, 438 distinct programs at 504 examples), s
2026-07-17 Count-Walk Replay Compound (Stage 8)
The believed-likelier outcome, delivered cleanly. 'Replay compounding' — retraining on the accumulated replay mixture — had lifted the aggregate score at every previous link in this model's build chain, so it was the saf
2026-07-17 Coding Fitness Harness (cognitive-core program)
Surprisingly good at writing single functions (HumanEval 76.2%, MBPP 56.5%) but weak at driving a multi-step coding task in a real agent loop (23%). The harness is validated: it agrees with an independent run to within 1
2026-07-17 → State-Track Installation (Stage 9)
The believed-unlikelier but hoped-for outcome landed. After the reliable 'just replay again' lever hit its ceiling, this tried a genuinely different lever: teach the model one new, universal skill — keeping a running tal
2026-07-16 Qwen35 4b Zero Root Lineage Rebuild
["The rebuild answered the provenance question with numbers. Retracing the six documented training steps from a truly blank starting adapter — same datasets, same seeds, same settings — produced a model with about ninety
2026-07-16 Repair-Verifier Signal Probe
The gate said no, cleanly. Handed two candidate repairs and the full failure evidence — a task solvable by mentally running each candidate through both trials — the model picked the working one 51.5 percent of the time w
2026-07-16 Clean-Path Statechain Extension
["Split verdict with a clean lesson. The state-tracking dose installed for the THIRD time on its third different parent — the program's most reliable trained effect — and the clean-lineage model beat the untouched base b
2026-07-15 Rank-Capacity Vehicle Cell
The trial could not answer the capacity question — by design. Its built-in guard required the known nine-point forgetting case to reproduce before trusting any comparison, and on this fresh screen that case measured only
2026-07-15 Interleaved-Replay Dose with Medium Pilot
The review round did not prevent forgetting: the dosed model lost nine to ten retained answers against both comparisons — almost exactly the cost of dosing directly — so the theory drawn from comparing old receipts is re
2026-07-14 → 15 Qwen3.5-4B Counterfactual Plan Reflection Transfer
Not known yet. The current checkpoint builds and checks fresh list, text, and register puzzles, plus a control where every plan is deliberately assigned to the wrong puzzle. No model has been loaded or trained.
2026-07-14 Policy-Supported Successful-Sibling Universal Curriculum
This version cannot run its second step. Across 624 first attempts it found 227 failures, but counting and routing had none and selection had only two; the plan required four failures in every skill. It therefore stopped
2026-07-14 Search-Scaffold Universal Curriculum
No. On 26 fresh paired cases, the staged-search model tied replay at 16 correct and trailed its parent at 18. All three parsed 23 answers and hit the limit three times; the candidate solved none of four execute/induct ca
2026-07-14 Residual-Skill Successful-Sibling Universal Curriculum
Grading the 3,600 retries found 855 short fully-correct ones, and nine of ten weak skills had plenty. But rule-guessing (induction) yielded a usable correct retry on only 2 of its 46 failed tasks, below the required four
2026-07-14 On-Policy Failure-Prefix Universal Curriculum
No. The unmodified parent solved 16 of 26 fresh tasks and equal-compute replay solved 18, while training corrections after the model's own real failures solved only 15. The repair model got none of the six targeted execu
2026-07-14 Failure-Selected Counterfactual Restart Curriculum
The data-selection stage passed: from 624 fresh attempts, the frozen rule selected 52 clean restarts, exactly four for each of 13 skills. Forty correct accuracy or cap failures and twelve correct-but-too-long cases are n
2026-07-14 State-Formation Branch Authorization Recovery
Yes for the no-model safety check: all six controls passed, the failed first attempt has a third preserved copy, and the two retry-blocking source paths were retired only after that archive commit passed both checks. The
2026-07-13 → 14 Close-Weighted Universal Commit Seam
No. On 26 fresh procedural cases, ordinary and close-weighted target training both produced 23 well-formed answers and three response-limit contacts. Close weighting scored 16 correct versus 15 for ordinary training, but
2026-07-13 → 14 State-Formation Analysis Recovery
Yes, the narrow recovery check passed. It accepts only the one registered file location, still rejects unsafe shortcuts, and has not yet examined any model result.
2026-07-13 Validation-policy counterexample curriculum
The test could not answer the question. Before the newly trained model was allowed to run, the starting model and the equal-size old-lesson control each fixed all 48 practice cases. The required gains were therefore impo
2026-07-13 Replay-Anchored Universal Curriculum Continuation
No at this dose. The designed mix passed its fresh synthetic screen but scored about 42% overall, below both the 44% mature policy and the 49% replay-only comparison. It also fell below base on one family. Replay-only wa
2026-07-13 Mid-Density Token-Matched Universal Curriculum
The 160-lesson stream improved fresh local accuracy from 17 to 19 of 26 cases, raised readable answers from 18 to 23, and cut answer-limit contacts from nine to three. It still missed the readability and length gates by
2026-07-13 Low-Density Token-Matched Universal Curriculum
No. Neither 40 nor 80 abstract lessons passed the fresh local screen. The stronger 80-lesson stream matched the inherited anchor at 54% accuracy and parsed 62% of answers, but still hit the answer cap 10 times; broad eva
2026-07-13 Qwen3.5-4B: Installing Universal Features via Designed Synthetic Curricula
Not with either tested training geometry. Continuing from the strong policy raised fresh synthetic accuracy from 50% to 69% and beat the untrained base overall, but it scored 31% aggregate versus 45% for the strong start
2026-07-13 State-Formation Capacity Adjudication
Not run yet. The reviewed test starts with three compact-update training runs. If any required state check misses, six matched controls become mandatory; the final three runs open only if the full-size version also misse
2026-07-13 Full-Rank Extra-R Delta: State-Carry Versus State-Bag
The run worked mechanically, but it did not settle the question. All 892 million full-size update weights trained and fit comfortably, yet macro task-mean joint-state accuracy was only 0.28% against a 40% requirement. At
2026-07-13 Semantic-policy headroom tournament
No rule produced a stable training target after a failed test: every one of 72 cases reached a correct patch. But before seeing test output, the model got zero of 54 ambiguous first patches fully right and never opened t
2026-07-13 Qwen3.5-4B Jacobian Counterfactual Branching
No. Across all three allowed strengths, the meaningful nudge made its assigned answer win only 4 of 48 times—exactly the one-in-twelve chance rate and identical to a generic nudge. The probabilities barely moved even at
2026-07-13 Qwen3.5-4B Early Text Hypothesis Forking
The experiment design and model-free checks now pass, but the model has not run. Review expanded the first draft from twelve operation names to twenty-four fully specified operations, added two fair late-hint comparisons
2026-07-13 Counterfactual evidence-acquisition curriculum
The run stopped at its first checkpoint-compatibility test. Across 48 frozen contexts, the starting checkpoint differed from the comparison anchor by 0.110735 centered logits, above the fixed 0.100000 limit. Entropy stay
2026-07-13 Qwen3.5-4B: The Compute-Optimal Confidence Policy (select + abstain + escalate)
Partly. Picking the answer with the highest single-token P(True) confidence is the best grader-free selector at every compute level, and abstaining below a confidence threshold trades coverage for accuracy cleanly — both
2026-07-12 Transaction-invariant recovery curriculum
Partly. Focused training lifted practice repairs from 52% to 82% and preserved the test-and-revise loop. But on different transaction APIs it reached 72% versus 70% before training, far below the required ten-point gain.
2026-07-12 Verifier-conditioned recovery banking curriculum
Yes — replaying real failures taught recovery, lifting success from about half of cases to more than nine in ten. But the best version also added a little "explain your fix" text, and that supposedly tiny slice actually
2026-07-12 State-Carry Versus State-Bag Counterfactual
The first matched test did not answer that architecture question because the low-rank update failed to learn the required running state. Carrying memory improved overall accuracy by only 4.3 points, with uncertainty span
2026-07-12 Qwen3.5-4B Same-Prefix Advantage Routing
Only when it replicates, and here one helper didn't. The test actually ran: the deep specialist's local edge held up on a fresh, separate batch, but the quick specialist looked strong on one batch of stuck points and the
2026-07-12 Locality-first recovery-reason interpolation
Yes on skill, no on shipping. One dial setting recovered from broken code 97% of the time, about 12 points above the act-only version and 15 above a matched-training baseline, while barely moving unrelated behavior. But
2026-07-12 Qwen3.5-4B Pareto Policy Integration
No. Retested on fresh, uncontaminated tasks, the version built for quick work actually lost at quick work by about two points, while the version built for long work won at both quick AND long tasks. One version quietly d
2026-07-12 Qwen3.5-4B Deep-Advantage MOPD
No. The deep specialist really was the better teacher on selected states, and copying it worked slightly better than copying the wrong teacher or training on matched non-winning states. But after four rounds the resultin
2026-07-12 Qwen3.5-4B Context-Local Jacobian Clamp
Yes, but only when the edit lands on the earlier token that first stores the word. There the model looked up the swapped word's digit on all 48 fresh puzzles, up from zero without the edit, and a wrong-word swap produced
2026-07-12 Qwen3.5-4B Balanced-Core Answer-Potential SFT
Not run yet — the reasoning bank is fully built (360 tasks, six competing selection rules staged) but no model has been trained or scored. The built test will fine-tune six copies, each fed reasoning chosen a different w
2026-07-11 Entropy-routed think-pivot optimization round 2
No. Gently pulling the better word up at 155 hand-picked wrong-turn moments was cleaner than shoving the bad word down, and it carried real signal, beating a scrambled-label control by about 14 points on fresh coding rep
2026-07-11 Qwen3.5-4B Specialist Policy Integration
No — we never found out. Each of four required skills had to gain ten points before merging, but scores top out at 100. One tool-use skill already sat at 99.4%, so its target of 109.4% was impossible. The experiment stop
2026-07-11 Interactive policy curriculum: oracle DAgger to execution-reward RL
No — it backfired badly. Success on the practice tasks fell from about 60% to 35%, and on tasks never touched in training from about 69% to 35%. It kept editing fluently but stopped running its checks: the verify-and-com
2026-07-10 → 11 Think-block FTPO round 1: outcome-conditioned pivot steering as an agentic install recipe
No. Nudging at those forks made the model worse, not better — success on fresh tasks fell about 4 to 8 percent instead of clearing the 5-point gain hoped for. The tell: feeding it deliberately scrambled labels did nearly
2026-07-10 Qwen3.5-4B Long-Horizon Answer-Potential SFT
Barely. That confidence signal does sort stronger reasoning above weaker about 60% of the time — better than a coin flip's 50%, and enough to lift a picked chain's success from 16% to 22%. But two dumb rules beat it: jus
2026-07-10 Qwen3.5-4B Answer-Potential Trace SFT
No. The score carried genuine signal — it tracked what the reasoning actually said, not its length or wording — but its top pick raised fresh-answer success only from about 13% to 20%, short of the useful margin needed t
2026-07-09 → 10 Gauntlet round 1: breadth-first agentic expert iteration
Mostly the second. On a blind benchmark the model scored about 14 percent, with six task types near zero, but it had usually reasoned correctly. It simply hit its thinking limit, restarted explaining instead of writing t
2026-07-08 → 09 Does the installable hypothesize-and-verify skill move the structure wall?
No. Fine-tuning the model on 1,476 worked guess-and-check traces doubled its success at the two-step depth it practiced on (lists jumped from 37% to 70%), yet did nothing one step deeper: three-step success stayed near 5
2026-07-07 → 08 Qwen3.5-4B: Can Confidence Replace the Verifier in the Banking Flywheel?
No. When training on answers checked by actually running the code lifted single-shot accuracy from 8% to 24%, confidence-filtered data — fifteen times purer than a random grab of the model's own outputs — landed right on
2026-07-07 Qwen3.5-4B: Can SFT Install the Skill of Induction?
Yes, but only when it thinks out loud. The trained model cracks brand-new hidden rules perfectly when it writes out its reasoning, yet collapses to worse-than-guessing — about 1 in 100 — when forced to answer in a single
2026-07-06 Qwen3.5-4B: When Does the Model's Structure Beat Brute Search? (depth-4)
No. Adding one extra dial — a sixteen-times-larger space of combinations — did not flip things. Exhaustive search stayed near-perfect at about 97 percent, while the model's knack for guessing the right combination from m
2026-07-06 Qwen3.5-4B: Learn from Your Own Failures (DPO)
No. The model already ranked its own correct answer above its wrong one 81% of the time — a sharp internal judge. But training it to favor the correct ones destroyed its writing: single-best-guess solving peaked near 5%
2026-07-06 Qwen3.5-4B: Does Banking Install STRUCTURE?
Yes, then no. Training lifted a 4-billion-parameter model from never proposing the right step-sequence (0%) to getting it right about half the time (51%) on brand-new tasks—a real new skill, not memorized answers. But if
2026-07-05 Qwen3.5-4B: Do Banking and Thinking Stack?
It depends on how far the goal is. One move away, the two boosts stack almost perfectly: a plain model picks the right move 27.5% of the time, extra training lifts that to 52.5%, and adding thinking reaches 85% — the exa
2026-07-05 Qwen3.5-4B: Bank the Thoughts
No. Training the model on its own successful reasoning taught it nothing beyond showing it the bare answers — both solved about 9 in 100 fresh three-step problems. But a short hand-written plan that builds the solution f
2026-07-01 Qwen3.5-4B Decompose-and-Compose Frontier
Yes — but not because the model got smarter. Taking three steps one at a time, with a tool that runs each and shows the result, solves about 2 in 5 versus 1 in 8 in one shot. The catch: blindly trying all 23 operations d
2026-06-30 → 07-01 Qwen3.5-4B Neurosymbolic REPL Substrate + Failure Profile
No. Seeing its real error barely helped: the fix-it loop solved 29% of puzzles versus 34% for simply drawing five independent attempts and keeping the best, at equal compute; the error message itself added just two tasks
2026-06-30 Qwen3.5-4B Thinking-Budget Scaling
Yes, but with a sweet spot. Turning on the model's built-in reasoning lifted the accuracy of the answer you would actually ship from 76% to 91% on basic Python tasks — a genuine capability gain, not just a wider pool of
~2026-06-30 Qwen3.5-4B Thinking-Budget Controller
For cost, yes; for accuracy, no. Drafting cheaply and thinking harder only when the draft fails the one visible example matches a generous fixed budget's accuracy (88%) using about a fifth of the thinking (113 versus 507
2026-06-28 Qwen Support-Contrastive Meta-ICL
Not by default. One tuned model scored 49% whether its worked examples were intact or scrambled, meaning it had memorized the task and ignored the examples entirely. A contrastive objective forced genuine reading: 50% wi
2026-06-28 Qwen Oracle-Distilled Acquisition Policy
No. The trained picker does read real signal: it beats revealing nothing (50 to 57 percent of tasks fully solved) and crushes a version fed scrambled answers (27 percent). But it lost to simply grabbing a varied spread o
2026-06-28 Counterfactual ICL Public Multiseed Gate
Yes, but not for the reason expected. Tuning tripled whole-task accuracy on real text tasks, from 20% to about 61%, stable across three training runs — and the model genuinely reads its examples: remove them and it colla
2026-06-28 Counterfactual Episodic ICL Posttraining
Yes. Untrained, a 4-billion-parameter model solved 23% of real text-transformation tasks perfectly; after this training, 57% — but only when it could see the prompt's examples. Scramble those examples and it fell to 17%,
2026-06-28 Qwen3.5-4B Tool State Policy LoRA
Surprisingly, yes, and with almost no learning. Trusting the program only when it passes a worked example and disagrees with the quick answer lifted accuracy from 56% to 66%, exactly matching the best any picker could re
2026-06-28 Qwen3.5-4B Live Tool DAgger
Only its cost, not its accuracy. Answering directly solved none of twelve unseen tasks; letting the model write and run code recovered two — about one in six — and spoiled nothing it already had right. But even a flawles
imported 2026-07-12 Qwen Slot Repair Distillation
No. A correct program almost always sits one or two edits away — a search that peeks at the answer lifts solve rates from about a quarter to roughly 86%. But the blind helper couldn't pick which edits to make: on reworde
imported 2026-07-12 Adaptive Cognitive Kernel
No advantage. The self-rewiring is genuinely doing ordered work: scrambling the operation order collapses its step-by-step accuracy from about 12% to 2%, and switching the rewiring off cripples it. But it never beats a p
~2026-06-27 Qwen 3.5 4B Balanced Discriminative Bridge
An even mix, clearly. Sixty evenly-spread ordinary examples across ten new program types lifted the model's success on unseen hard problems from 60% (with no examples at all) to 99% fully solved. Hand-picking only the tr
2026-06-26 Qwen3.5-4B Pass@k Coverage RL
No. Retraining the model to spread its tries across different problems actually lowered coverage: it solved about 44% of unseen coding problems within four tries, versus about 69% from simply raising the randomness dial
2026-06-26 Qwen3.5-4B OPSD Pressure Locality Audit
No. At the exact spots where correct code diverges from code that passes surface tests but is secretly wrong, the reference hint adds essentially nothing — scoring no better than a scrambled, meaningless hint. The hint o
2026-06-26 Qwen3.5-4B Offline Hard Negative Coverage DPO
It depends — and even the gentle version failed its own bar. A light touch matched the task-solving reach of generating twice as many candidate answers at roughly half the compute, and beat a shuffled-pair placebo. But i
2026-06-26 Qwen3.5-4B Constrained Coverage DPO
Not quite. The nudged model solved 62% of problems within four tries versus 58% for the untrained model, and kept its first-try accuracy — a real, cheap gain. But simply doubling to eight tries solved 67%, still more. Th
2026-06-25 → 26 Qwen3.5-4B Sampler Portfolio Scheduler
In theory yes, in practice no. A flawless chooser that knew which style would crack each problem solved 75% of coding tasks at the cheapest run's cost, while just doubling tries from one style reached 67% at twice the co
2026-06-24 → 26 Qwen3.5-4B Oracle Probe Synthesis MDP
It's the menu. Just curating which eight test inputs the model chose from raised success from about 43% to 49% — a bigger jump than any training gave. Supervised coaching added a bit more (48% to 51%); preference- and re
2026-06-25 Qwen3.5-4B Verifier-Guided Self-Improvement Report
No. After a four-billion-parameter model retrained on its own test-passing code, its success on unseen problems barely moved, going from about 65% to about 65% (a hair lower). Retraining made its several attempts look mo
2026-06-25 Qwen3.5-4B Trained vs Frozen Repair MDP Report
Retry from scratch. Given the same compute budget, a few more fresh attempts rescued 5 of 57 stuck problems, while a fixer trained to patch broken code rescued only 2 — and its repairs secretly failed the hidden tests ne
2026-06-25 Qwen3.5-4B Strategy Token Diversity LoRA
No. Feeding the model labeled coding tactics recovered 37.5% of the problems it first failed, slightly below plain extra sampling at the same cost, which recovered 41.7%. Tellingly, scrambling the labels so they meant no
~2026-06-25 Qwen3.5-4B Oracle-Distilled Semantic Verifier
Yes, but only on home turf. On the problem set it trained on, the trained judge picked a genuinely-correct program 81% of the time, up from 72% for the same model untrained and just 44% for grabbing the first candidate t
2026-06-24 Qwen VM-ECHO Trace Distillation
Mostly no. The model got far better at predicting execution, with reading a running program's top value climbing from under 1 percent correct to 43 percent, but that rarely improved the programs it wrote. First-try accur
2026-06-24 Qwen VM-Agent ECHO QLoRA
Only the acting helped. Editing-and-running in a loop lifted the share of tasks solved from 10% at a blank start to 43%, beating a single one-shot guess near 37%. But adding a second job, predicting the program's output
2026-06-24 Qwen Search-Augmented Rollout Distillation
No. An automatic search found a verified correct fix for 98% of the dead-ends the model wandered into, yet retraining on those single fixes matched or trailed the simpler training on four of five test sets. The model cou
2026-06-24 Qwen Recurrent VM Repair Policy
Yes, but only partway. Letting the model run its program, read the output, and fix one line at a time roughly tripled accuracy, from about 11% to 34% on the main test and 16% to 40% on reworded prompts. But a perfect edi
2026-06-24 Qwen In-Policy VM-ECHO Distillation
Only partly. It became excellent at predicting mechanical outcomes, like how deep a program runs (about 92% right), but stayed no better than a coin flip at judging which program is actually correct. So it could not rank
2026-06-24 Qwen Fuyu VM GRPO-ECHO
No. Copying worked solutions alone solved about 10% of tasks; one round of reward-based self-coaching dropped that to 7-8%. The coaching produced encouraging signals — it could rank good fixes over bad ones 80% of the ti
2026-06-24 Qwen Dense-State DAgger VM Agent
Mostly yes. Teaching the model to make one edit at a time, then correcting it on the messes it made, roughly doubled accuracy on mixed tasks (22% to 41%) and won on four of five task types. But it lost on ordinary tasks
2026-06-24 Qwen Counterfactual Trace Preference Distillation
Barely. The self-grader learned to favor programs that run without crashing, but it identified the truly correct one only about 15% of the time, against a 41% best-possible ceiling. On fresh questions it picked worse tha
2026-06-24 Qwen Action-Conditioned VM-ECHO Policy Iteration
Barely. Learning to grade drafts by their run results nudged picking accuracy only from about 10% to 11%, far short of the 37% reachable by always choosing the best available draft. It reliably picked programs that ran,
2026-06-24 Qwen3.5-4B Oracle Process GRPO
Yes, but with sharp limits. Teaching the model to copy a flawless test-picker lifted its success from about a third of puzzles to 43%, versus roughly 31% for picking blindly. Layering on preference-based and reward-based
2026-06-24 Qwen3.5-4B Learned Active Trace Policy
It depends. On the main test set a simple even-splitting rule beat the trained picker after one extra input — 91 percent of programs fully correct versus 87 — and the best-possible choice reached 97 percent. The picker d
2026-06-24 Qwen3.5-4B Inventory Shortlister Training
No. Even after extra training, and even allowed to submit its 1,024 strongest paired guesses, it got exactly zero right — no better than the untrained model, and no better than a control with the tool labels scrambled. T
2026-06-24 Qwen3.5-4B Deployable Information Ceiling Sweep
It's the clues. On the hard hidden rule, the plain strategy got just 4% right when starved of tests and clues, far below the 74% of a rival who secretly knew the answer. But allowing more tests lifted it to 86%, and more
2026-06-24 Qwen3.5-4B Bucket-Belief Probe Ranker
Barely. After training, the 4-billion-parameter model solved 50% of puzzles within three tests, versus 49% for a simple no-learning rule that just picks the cleanest-splitting test, essentially a tie. Even limited to tho
2026-06-24 Qwen3.5-4B Adaptive Evidence Budget Policy
Yes. Trained just for this single decision, the model matched the accuracy of running all ten checks — solving about 92 of every 100 tasks — while using only about five checks on average, near a perfect-hindsight stopper
2026-06-23 Qwen On-Policy Repair-to-Compiler
Yes, but the self-correction isn't the secret ingredient. On brand-new requests the model climbed from about 29% correct programs to 99% after training on its own corrected drafts. The catch: training on plain correct pr
2026-06-23 Qwen LoRA Typed-Bytecode Trace Compiler
Yes — but the win came from the teaching material, not from adapting the model. Fed fully worked recipes, it wrote a runnable recipe that reached the right answer about 68% of the time, versus only 15% when taught with f
2026-06-23 Qwen Iterative Repair Policy
Yes. The frozen model alone got about 30% of programs exactly right; editing one step at a time lifted that to 53% on fresh problems, closing roughly 38% of the distance to the best a perfect fixer could reach (89%). The
2026-06-23 Qwen Hidden VM On-Policy Canonical Repair
No. Training the model on automatically corrected recipes reached 61% on new tasks, versus 59% for plain training — a 2-point gap that is basically noise, and it left longer tasks no better. The corrections are genuinely
2026-06-22 Qwen Verifier-Guided Slot Repair
Yes, mostly, but with a catch. A small model copying 24-step calculations got only about 27% exactly right on its own. A checker that knows the correct running number after every step, allowed to swap one or two bad step
2026-06-22 Qwen Teacher-Distilled Slot Compiler
No. A model trained to copy numbers and operations out of text and run a 24-step calculation got 27% of final answers exactly right; adding the pointing signal landed at 28%, a tie. Worse, agreement between two rewording
2026-06-21 Qwen LoRA Parser Compiler
Partly. With step-by-step coaching, a small four-billion-parameter model's hidden states became a readable program: it named the starting number every time and picked the right operation about 98 percent of the time, whi
2026-06-21 Dense Teacher Distillation Experiment
No. Even with a flawless teacher revealing the exact set of still-possible answers at every step, the fixed-size memory learned only a rough approximation. The best version placed 52% of its confidence on the correct fin
2026-06-19 → 20 Execution-Conditioned Repair LoRA Experiment
No. On bugs built from the same templates it practiced on, the fixer repaired all 60 of 60 cases, versus 11 of 60 with ordinary patch training and 6 of 60 with no training at all. But on bug types it never saw, every met