When stronger conditional reasoning fails to transfer: an independent-prefix RLVR bridge on Qwen3-0.6B

Research question and distinction

A small model can answer more questions when shown one of its own verified solutions. That does not establish that a model trained on the resulting continuations answers new questions better without that information. We separate these two tests on Qwen3-0.6B-Base after a 50-update GRPO warm start (seed 17041).

STaR [1] already combines successful native generations with answer-conditioned rationalizations of failures, removes the hints for fitting, and repeats data generation while retraining from the original model. Its rationalization ablation is task-dependent (GSM8K 10.1% to 10.7%); it does not establish the behavior of our warmed 0.6B setting. Our construction follows verified expert iteration (ReST-EM [2]) and teaching at student states (SDPO [3], DAgger [4]). Our actor uses hard targets, unlike SDPO's distributional feedback. ReTeach [5] also conditions a self-teacher on successful retry history, but distills on prefixes of the original rollout rather than training directly on the successful retry text. The differences in size, native thinking skill, teacher lag and evaluation budgets prevent transferring their positive results to our warm-started 0.6B Base model.

SDPO includes Qwen3-0.6B in its scaling study and reports greater robustness from mixing scalar GRPO and dense teacher advantages for that weak model. Its principal Table 12 settings disable thinking. This differs from ReTeach's thinking-enabled teacher and from our warm-started Base checkpoint; those distinctions should not be collapsed into a general claim that prior work only studies 8B thinking models. SDPO also evaluates SFT on successful self-teacher generations, directly relevant prior art for hard targets.

Snell, Klein and Zhong [6] formalized same-model context distillation with different teacher/student templates and an output extractor. Their implementation already uses soft token KL, approximated by empirical labels, while their prefix distribution differs from later on-policy methods. Our hard accepted-suffix experiment is an adaptation of this established framework.

Re-ReST [7] is direct prior art for hard repaired targets: a separately trained reflector conditions on unsuccessful attempts and environment feedback, verified repairs augment native successes, and the actor is fitted without the reflector in its inference path. Some reported arms use same-family models without added GPT demonstrations; other arms add external demonstrations and must be distinguished. Our fixed checkpoint supplies both source roles and uses one independently drawn prefix, without a separately adapted reflector. Repair followed by verification and ordinary actor fitting is established methodology.

MARGE [8] already samples verified continuations from intermediate states of own-model solutions and learns from their outcome differences. It selects guiding responses by estimated difficulty and refreshes them across rounds. Our single independently drawn prefix, separately supplied successful context, and hard success-only loss form a different fixed pipeline; intermediate-state exploration itself is established prior art.

The relevant local predecessors are broad verified self-training [9], native/inserted-state fitting [10], the low-success information ledger [11], and train/twin transfer [12]. They make a distinction between easier conditional generation, fitting training examples and improving native held-out answers. Our proposed contribution is the tested connection between an independent student prefix, a verified contextual continuation and a context-free fitted endpoint. It is not a claim that verified self-training or privileged self-teaching is new.

Source roles and prior feasibility

The original source bank contains 6,400 training questions with eight native samples each, generated at temperature 0.8, top-p 0.9, and a 1,024-token cap. We selected 256 pilot identities before inspecting their outcomes for this purpose. Draws 0–3 supply the first boxed-correct solution ending in EOS, if one exists. Draw 4 supplies its first 64 tokens irrespective of its eventual grade and must not have ended within that prefix. These are independent draw assignments conditional on the same question and model; their values and availability strata need not be independent.

For 158 eligible questions, we generated four continuations in each of three conditions: native question and prefix; an empty feedback template and prefix; and the same template containing the verified solution and prefix. Every continuation receives a full 512-new-token budget. The privileged prefill is longer and charged separately. Grading uses only the decoded student prefix and new suffix, excluding the entire privileged solution prompt.

Mean correctness was 0.662975 for native continuation, 0.659810 with the empty template, and 0.816456 with solution context. Solution minus empty was +15.665 percentage points (pp), with paired eligible-question bootstrap 95% interval [10.918, 20.570]. Solution minus native was +15.348 pp [10.756, 20.095]. The pilot generated 1,896 trajectories and 600,032 tokens, charging 3,855.365 helper seconds. This is incremental cost: the shared parent bank additionally generated 28,871,889 tokens and charged 43,579.5 helper seconds. Final reporting must include EOS, accepted yield, and prefill work from the original audit.

A diagnostic found exact extracted-answer equality with the context answer in 81.5% of solution-context responses, versus about 63.1% of native and empty-template responses. Equality is compatible with copying and with independently producing the same correct answer; it does not identify a causal copy fraction. Prefix answer exposure is another possibility. The measured result is a conditional continuation improvement.

A post hoc check applies the new first-success retention rule to the completed pilot only. Native yields 130 eligible targets and teacher yields 139: 125 questions overlap, 14 are teacher-only, 5 native-only, and 14 neither. Mean retained suffix length is 273.44 native versus 269.38 teacher tokens. Only three retained suffix token sequences are identical on the shared 125 questions. Low exact agreement between independent samples does not by itself establish different conditional target distributions. Thus the large mean-per-sample advantage becomes a much smaller coverage difference after verification. Both retained sets are correct by construction; a fitted contrast combines coverage and trajectory distribution, rather than inheriting the raw correctness gap. This check does not change the frozen new-tranche retention or gate.

Scope of the preceding actor result

A preceding actor study fitted original successful native traces, with or without masking their first 64 tokens. It was initially described too broadly as a teacher-to-actor test. A source audit showed that it used no teacher-generated suffixes at independent student prefixes; that public interpretation was corrected in the discussion. Its greedy error bins were also incorrectly called sampled-zero bins and were corrected. The current experiment supplies the previously missing source-to-actor link. The preceding study is context, and its records are not part of this paper's evidence archive. The current whole-trace arm re-executes the same 636 full targets and question order from the same warm checkpoint; it is a repeated control, not an independent data or initialization replication. The new scientific link lies in the freshly generated native and contextual suffix targets at independent prefixes.

Actual bridge experiment, fixed before new generation

The experiment reuses the original 1,024 selected training identities, excluding all 256 pilot identities and every protected development or reserve identity. There are 636 eligible contexts and independent student prefixes that have not ended. We collect four native and four solution-context continuations per question: 5,088 trajectories in total, each with 512 new tokens at temperature 0.8 and top-p 0.9. The template, source checkpoint, and prompt/token concatenation follow the pilot. No larger model or researcher-written solution enters supervision.

A pre-generation CPU audit found no extractable boxed answers in these 636 prefixes. Thirty match the first 64 tokens of the successful context, and the median common-prefix length is 10. This does not exclude unboxed answer exposure or copying from the teacher's deliberately supplied solution. Eligibility is strongly selective: 81 of 87 Level 1 questions have a context, versus 101 of 293 Level 5 questions. The source comparison applies to questions covered by a warm-model context, rather than questions with no success in draws 0–3.

In each source condition, retain the first boxed-correct EOS suffix in sample order 0–3. Questions without a target remain in the ledger. Fitting requires at least 128 teacher-covered questions and a positive lower 95% bound on teacher minus native mean@4 over all 636 eligible questions. This source gate governs spending; it is not evidence that an actor has learned.

Three actors start from the same warm checkpoint and fit teacher suffixes, native suffixes, or the original whole successes. The first two see only the native question and independent student prefix, with loss on new suffix tokens including EOS. The whole-trace actor sees the native question and receives loss on the original verified trace. All use the same 636-question order, 80 updates, batch size 8 (4 in the final batch), constant AdamW learning rate 2e-6, weight decay 0.01, gradient clipping at 1, and the supplied BF16/FP32 parameter precision.

Missing targets contribute zero without renormalizing the batch denominator. Explicit zero gradients preserve AdamW's momentum and weight-decay clocks. Matching questions and update counts therefore does not match token exposure or source cost. Teacher/native coverage differences are part of the pipeline intervention, not an isolated effect of target content.

For a minibatch B and retained target set E_a, the actor objective is

$$L_a(\theta)=-\frac{1}{|B|}\sum_{i\in B\cap E_a}\frac{1}{|y_{ia}|}\sum_t\log p_\theta(y_{ia,t}\mid q_i,z_i,y_{ia,<t}).$$

For the whole-trace arm, omit z_i and use the original full success as y. This per-target length normalization differs from pooled token likelihood. Hard imitation initially contacts a student state at the fork; later prefixes follow the accepted continuation. It is not on-policy feedback at every future actor state.

First-success retention also changes the training measure. For independent draws with acceptance event $E$ (boxed-correct and EOS), success probability $p_a(x)$, and a zero contribution if no target is found, standard rejection-sampling algebra gives

$$\mathbb E[\text{retained loss}\mid x] = [1-(1-p_a(x))^4]\,\mathbb E_{q_a}[\ell(Y)\mid E,x].$$

The native-versus-teacher source comparison changes both the feedback template and supplied information; it is a pipeline comparison, not an isolated information intervention. The earlier empty-template pilot supplies the narrower information-plus-context-length comparison. The teacher can change both coverage weighting and the conditional accepted target law. A raw success-rate improvement alone guarantees neither a different accepted target law nor a native actor gain. This is an interpretation of our first-success rule, not a new self-distillation theorem. For example, an idealized teacher that only exponentially tilts the binary acceptance event leaves the conditional accepted sequence law exactly unchanged. It can improve raw correctness while changing only finite-budget question coverage after rejection filtering. This illustrates a possible failure of source advantage to transfer; it does not identify the behavior of our contextual teacher.

The development endpoint uses native greedy decoding with a 2,048-token cap on the same balanced 1,008-question panel used earlier: four chunks of 252 rows and batch size 8. The warm score of 445 correct is reused with its exact execution layout. Paired question bootstrap uses 20,000 draws, resetting seed 9917041 for each contrast. The spending gate requires teacher minus warm to be at least +3 pp and teacher minus each fitted control to be at least +2 pp, with all three lower 95% bounds positive. With discordance 0.15, a normal approximation requires about a 3.42 pp true effect for 80% power of one positive lower bound at N=1,008; power for the conjunction is lower. These gates will not be weakened after results.

A pass leads to nominal and development-calibrated matched-temperature sampling, independent warm/source replication, and a genuinely comparable-work ordinary RLVR comparison before MATH-500 or another final benchmark. A fail closes this fixed bridge budget without claiming general impossibility. None of these later endpoints is currently measured.

Execution and resource limits

The shared warm initialization used 50 updates and 400 rollouts. Its saved summary reports 465.181 training-loop seconds, and the earlier author-run training analysis records 140,446 generated tokens. That timer excludes helper and setup overhead and must not be treated as the same clock as the later helper totals. The compact archive includes these records but does not independently replay warm training.

Each GPU worker reserves one NVIDIA GeForce RTX 4090 through gpu-run and exits within 3,600 seconds. All 20 actual source configurations record PyTorch 2.5.1+cu121 and that GPU model; the shared pool contains eight RTX 4090 devices, with at most one used by this project at a time. The helper-time ceilings are 18,000 seconds for source collection, 1,800 for fitting, and 18,000 for readouts. Every failed attempt is retained and charged. A subprocess symbolic grader with a 5-second deadline and exact inequality prechecks returns a boolean grade or raises unresolved; no timeout becomes zero. No scientific worker is silently retried and incomplete endpoints are not imputed.

Report generated/scored tokens, padded prefill/incremental positions, attention key slots, full forward/backward positions, accepted question coverage, updates and helper time separately. An earlier ordinary continuation was reported separately in the same discussion. It differs in question selection, order, objective, and work. It is neither a matched control nor part of this paper's archived results. A passing bridge still requires a genuinely comparable-work ordinary RLVR comparison.

Greedy execution is sensitive to batching in this implementation, as also documented by a separate community study [13]. The warm and fitted readouts here use the same predetermined chunks and batch size. Item-bootstrap intervals remain conditional on this warm/source/fitting realization; they do not measure training-seed uncertainty or establish reproducibility of the recipe.

The task's proposed fast-policy feedback loop has a direct precursor in Chung's thesis [14, §5.4]. It reports that Thinker improves the augmented multistage system while explicit supervised projection of successful summaries into the fast policy was unsuccessful. The thesis proposes a mismatch between summary trajectories and fast reasoning as one possible explanation; its narrative does not isolate that cause or supply a quantitative bound on projection methods. Our independent prefix gives a hard target contact with a native student state, but subsequent target tokens still follow the accepted continuation. Even a positive result would establish one working construction, not prove that distribution mismatch caused the earlier failures.

Completed source results

The full source audit reconstructed and regraded all 5,088 continuations. Mean@4 is 0.636006 for native continuation and 0.809748 for solution context, a +17.374 pp difference with paired-question bootstrap 95% interval [14.819, 19.929]. The frozen source gate passes. This confirms the direction of the earlier pilot on a disjoint question tranche with the same warm checkpoint; it does not constitute an independent warm-seed replication.

| Quantity | Native | Solution context | |---|---:|---:| | Correct continuations / 2,544 | 1,618 | 2,060 | | EOS continuations / 2,544 | 1,956 | 2,064 | | Boxed-correct EOS continuations | 1,556 | 1,991 | | Questions with a retained target / 636 | 490 | 551 | | Mean retained suffix tokens | 270.98 | 276.24 | | Total retained suffix tokens | 132,778 | 152,206 | | Generated tokens | 811,967 | 800,027 | | Padded prefill positions | 379,956 | 1,492,636 | | Padded incremental positions | 908,624 | 862,260 | | Dense prefill query-key slots | 68,199,612 | 1,001,961,268 | | Padded incremental key slots | 329,407,076 | 741,853,880 |

Retention overlaps on 469 questions, with 82 teacher-only, 21 native-only, and 64 neither. Thus the 17.37 pp per-sample correctness advantage becomes 61 additional covered questions, or 9.59 pp, under the four-attempt first-success rule. Nine pairs of retained suffixes are token-identical among the 469 overlapping questions; this is not an identification of conditional target laws. Native retention selects draws 0/1/2/3 on 389/55/27/19 questions; teacher retention selects them on 492/37/16/6. There are no all-missing fitting minibatches in either arm. The summed accepted fractions across 80 minibatches are 61.625 native and 69.25 teacher, versus 80 for full coverage. These are objective coefficients, not measured gradient norms or effective update sizes.

Incremental source collection generated 1,611,994 tokens and charged 9,112.381 helper seconds across all 20 completed jobs. The longer teacher input has substantially more prefill and attention work despite slightly fewer output tokens. The earlier parent bank and pilot costs remain additional; the source improvement is not an end-to-end efficiency claim.

Completed fitting and native readout

All three actors completed the predetermined 80 updates with seed 9817041. The final checkpoint hashes and the complete fitting-work ledger were bound before any actor readout; the audit passed. This audit checks records and weights, not an independent numerical replay of the optimizer.

| Fitting quantity | Native suffix | Teacher suffix | Whole trace | |---|---:|---:|---:| | Nonzero target questions | 490 | 551 | 636 | | Missing target questions | 146 | 85 | 0 | | Scored completion tokens | 132,778 | 152,206 | 261,634 | | Forward/backward positions | 202,107 | 233,552 | 315,919 | | Helper seconds | 53.203 | 59.000 | 65.419 |

Total fitting charged 177.622 helper seconds. Source acquisition dominated fitting cost in this pipeline; this observation does not compare its efficiency with ordinary RLVR.

Native endpoint and decision

All twelve development readout chunks completed with return code zero under protocol hash 6ad7c68f8174c2d1ef9475bcc58c5f1a1c763e3785eb7402b33da95e4c42fa7e. On the fixed 1,008-question greedy panel, the contextual-teacher actor scored 443/1008 (43.95%), versus 445/1008 (44.15%) for the reused warm checkpoint, 454/1008 (45.04%) for the native-suffix fitted actor, and 449/1008 (44.54%) for the whole-trace fitted control.

| Contrast (teacher minus) | Change | Paired bootstrap 95% interval | Acquisitions / regressions | |---|---:|---:|---:| | Warm | -0.20 pp | [-2.38, 1.88] pp | 59 / 61 | | Native fitted control | -1.09 pp | [-3.37, 1.19] pp | 60 / 71 | | Whole-trace fitted control | -0.60 pp | [-2.88, 1.69] pp | 63 / 69 |

The conjunction gate required at least +3 pp versus warm, +2 pp versus each fitted control, and positive lower bounds for all three intervals. It therefore fails. This closes the fixed hard-target bridge budget. The result does not show that contextual self-teaching is impossible, that source quality is irrelevant, or that dense/on-policy feedback would fail. It shows that this one warm-start, one-source realization and 80-update hard-suffix adaptation did not produce the required native greedy gain.

The contextual source advantage remains real at the conditional-generation level (+17.374 pp mean@4 on 636 eligible questions), but it did not transport through this fitting recipe. The native fitted control's +0.89 pp over warm also has a paired interval crossing zero, while the whole-trace control is +0.40 pp; neither is evidence of a replicated capability gain. No matched-temperature sampled endpoint, independent warm/source replication, comparable-resource ordinary-RLVR control, MATH-500 readout, or second benchmark was run under this failed gate. These are deliberate stopping consequences, not missing imputation.

Reproducibility and evidence scope

The compact supplement is designed to include all extracted official and boxed source candidates, grades, EOS flags and lengths, together with every native development answer vector once readout is complete. It contains the frozen selection, generation, fitting and evaluation recipes, source and fitting work receipts, and a CPU checker that regrades extracted candidates and reconstructs the reported statistics. Supplied task data and tokenizer hashes bind the evaluator inputs. An unresolved symbolic grade stops checking rather than becoming an incorrect answer.

The station's supplement limit prevents including every full trajectory in this compact archive. Full-text samples were selected by fixed positions before complete outcomes: the first two eligible source questions in each tranche, and development indices 0, 63, 126 and 189 within each chunk for every arm. Public independent re-extraction is therefore limited to those samples. Hashes identify the omitted raw originals but do not make them independently inspectable. Our local source audit re-extracted and regraded every raw source record; that is an author-run check. This distinction limits the public audit and must accompany any correctness claim.

A supplied materializer reconstructs a fresh source bank and teacher-to-actor run from the original task code and a newly trained warm checkpoint. The historical seed is 17041; an independent replication must declare a distinct warm seed and regenerate that checkpoint's warm readout. Reusing the historical 445-answer vector with new weights would invalidate the comparison. Portable input reconstruction has passed CPU checks; no fresh independent neural replication has been performed. Baseline and vendor source retain Apache-2.0 attribution, and added code uses the same license. Model checkpoints are not redistributed.

References

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[14] Ming Hay Chung. Learning to Plan with Reinforcement Learning. PhD thesis, University of Cambridge, 2026, §5.4. https://doi.org/10.17863/CAM.129818