Datasets:

ML-Intern-lab
/

pre2post-chess-replication

---
license: mit
tags:
- ml-intern
- replication
- chess
- scaling-laws
- reinforcement-learning
---
[![Built with ML Intern](https://huggingface.co/datasets/huggingface/badges/resolve/main/built-with-ml-intern-sm.svg)](https://hf.co/chat?mode=ml-intern)

# Replication: "Understanding Reasoning from Pretraining to Post-Training"

Reduced-scale replication of core claims from **"Understanding Reasoning from
Pretraining to Post-Training"** (Shen et al., arXiv:[2607.16097](https://arxiv.org/abs/2607.16097)),
using the authors' released checkpoints, benchmark and code
([pavelslab-nyu](https://huggingface.co/pavelslab-nyu),
[Pre2Post-Chess-RL](https://huggingface.co/Pre2Post-Chess-RL),
[GitHub](https://github.com/pavelslab-nyu/pre2post-chess)).

**Scope (agreed with the task owner):** T0 = rebuild + calibrate the eval
harness against the authors' protocol; T2 = replicate the joint pretraining–RL
scaling law (their Fig. 3); T4 = replicate the move-level mechanism analysis
(their Sec. 4.1 / App. H). Faithful but reduced-scale; no training of our own.

## T0 — Eval harness (calibrated)

We reconstructed the authors' exact evaluation protocol from their released
code (verl fork rollout worker, `reward_function_multiturn.py`,
`sft/evaluation/multiturn_puzzle_evaluator.py`):

- **SFT protocol** (`code/eval_chess.py --protocol sft`): natural-CoT
  generation up to 1024 tokens from `{pgn}<T>`, stopping at `</T>`; then a
  move loop (≤32 tokens per move, stop at `<call_env>`), env replies injected
  after `<call_env>`, ≤5 solver moves, temp 1.0. Episode success = every
  solver move matches the ground-truth UCI line (= paper's pass@1).
- **verl protocol** (`--protocol verl`, for RL checkpoints): fixed 1024-token
  thinking budget where a premature `</T>` is replaced by `<sep>` and thinking
  continues; forced `</T>` at budget exhaustion; answer phase (≤1536 tokens,
  ≤6 env calls); extraction = first LAN move after `</T>`, else last LAN move
  in the segment (the authors' fallback).
- Batched generation uses left padding (verified exactly equal to
  unbatched greedy generation); right padding was verified **incorrect**.

Calibration on released checkpoints (B1+B2, 25/bin, k=8, temp 1.0):

| checkpoint | protocol | pass@1 | pass@8 | first-move acc |
|---|---|---|---|---|
| SFT `model_20m_5.3B` | sft | 1.5% | 8% | 5.3% |
| SFT `model_680m_16B` | sft | 2.5% | 12% | 15.3% |
| RL `model_20m_5.3B` @ step 5000 | verl | 3.3% | 12% | — |

This already reproduces three qualitative claims: RL improves pass@1 without
improving pass@k; larger pretraining improves move quality; absolute pass@1 is
percent-level, consistent with the paper's own R₀(L) = 14.62·10^(−4.30·L) fit.
Dominant failure mode at 20M: illegal committed moves (~78%), matching the
authors' own `illegal_move` failure category.

## T2 — Joint pretraining–RL scaling law

**Data.** 48 RL evals across the full 20M family (10 pretraining budgets
× up to 5 RL steps; steps 100–5000) on the paper's fitting bins **B3+B4**
(`results/t2/`), plus a focused high-power sweep on **B1+B2** (6 pretraining
levels × 3 RL steps, 640 draws/point; `results/t2b_*.json`). Pretraining
validation loss L(N,T) computed on 3000 held-out Lichess 2023-01 games
(460k tokens per checkpoint; `results/loss/`) — a *proxy* for the authors'
unreleased val split.

**Finding 1 (B3+B4 floors out).** On the paper's fitting bins, the entire 20M
family measures 0–1% pass@1 (B4 = 0.000 in all 48 evals; only 40B@step4900
reaches 1%). At our measurement scale (400 draws/point vs the paper's ~8900)
these bins cannot resolve the correlation. The paper used B3–B4 to avoid
saturation of *larger* models; at 20M with our draw budget nothing saturates,
so we moved the high-power sweep to B1+B2.

**Finding 2 (claim 4a — pretraining loss predicts post-RL pass@1: reproduced
directionally).** On B1+B2, measured pass@1 at fixed RL compute (step 5000)
vs our L: **Spearman ρ = −0.54, Pearson r = −0.63** (n = 6; lower pretraining
loss → higher post-RL pass@1). The paper reports ρ = −0.93…−0.99 via R_ref
extrapolated to C_ref = 10²⁰ FLOPs; our extrapolated R_ref is noise-dominated
(ρ = +0.60, wrong sign) because each per-run slope is fit from 3 points with
±0.7% per-point noise and then extrapolated ~3.5 decades. We therefore treat
the non-extrapolated correlation as our replication of 4a and report the
extrapolation failure as a scale limitation.
Measured points (B1+B2, step 5000):
| pretrain tokens | L (ours) | pass@1 |
|---|---|---|
| 0.53B | 0.704 | 2.0% |
| 1.6B | 0.588 | 3.3% |
| 5.3B | 0.531 | 2.5% |
| 11B | 0.513 | 3.6% |
| 32B | 0.488 | 4.4% |
| 53B | 0.480 | 2.8% |
**Finding 3 (claim 4b — RL slope grows with log pretraining tokens: not
resolvable).** Per-run slopes B from 3-point curves at our noise level are
unidentified (Pearson r(B, log T) = −0.66, wrong sign, driven by one noisy
point). The paper's r = +0.84 over 36 runs with ~8900 draws/point is outside
what this budget can resolve.
## T4 — Mechanism analysis (RL policy evolution)
Induced root-conditioned move policies π̂(a|s) via K=10–12 verl-protocol
trace rollouts per puzzle and teacher-forced move scoring (paper: K=128),
12 puzzles each from B1 (easy), B4, B5 (hard); SFT vs RL steps 100/300/500;
Table-13 categorization (top-k=3, ε_tail=0.05). Counts per bin
(`results/t4_mechanism.json`):

| category | B1 (rl100/300/500) | B4 | B5 |
|---|---|---|---|
| gt_amplification | 1/2/2 | 4/3/4 | 2/3/3 |
| tail_discovery | 3/1/4 | 0/2/0 | 2/2/0 |
| gt_regression | 1/2/1 | 0/1/1 | 0/1/3 |
| topk_correction | 1/1/1 | 0/0/1 | 0/0/1 |
| wrong_mode_amplification | 0/1/0 | 2/1/3 | 2/1/1 |
| other | 6/5/4 | 6/5/3 | 6/5/5 |

**Partially reproduced / not resolved.** All five categories of the authors'
taxonomy occur, including tail discovery on hard bins at intermediate RL
steps (2/12 on B4 at step 300; 2/12 on B5 at steps 100–300). But the paper's
headline contrast (amplification concentrated on easy puzzles, discovery on
hard ones) is not resolved at K≈12 rollouts and 12 puzzles/bin: our dominant
consistent signal is amplification on B4/B5, and single-count swings dominate.
K=128 and larger puzzle samples would be needed for a decisive test.

## Deviations from the paper

1. **Validation loss is a proxy** (held-out Lichess 2023-01 games, our
   tokenization/windows) — absolute L values are not comparable to the
   authors'; correlations use our internally consistent L.
2. **Measurement scale**: 400–640 draws/point vs the paper's ~8900; K≈12
   rollouts vs 128 for T4. This is the dominant limitation and is the
   explanation we propose for the un-resolved claims, since the harness
   itself is calibrated against the authors' code paths.
3. **Bin substitution for the high-power sweep** (B1+B2 instead of B3+B4),
   justified above.
4. 20m_21B/40B RL runs excluded from loss correlations (no released
   pretrain checkpoint for those budgets).
5. RL-compute C per step estimated as 10·N·2048·(L_prompt+L_resp) with
   measured prompt length and assumed response length (paper App. D);
   slopes are unaffected by the constant.
## Artifacts
- `code/` — eval harness, val-loss computation, scaling-law fit, mechanism analysis
- `results/t2/` — 48 B3+B4 RL evals + B1+B2 evals (`t2b_*` tags)
- `results/loss/` — held-out pretraining loss for 32 checkpoints
- `results/fit_results.json` — all fit statistics
- `results/t4_mechanism.json` — induced policies + category counts
- Calibration JSONs: `results/t2/…` (see T0 table; B1+B2 25/bin runs)
## Citation
Paper: https://arxiv.org/abs/2607.16097 — Shen, Li, Rahman, Sun, Goldblum,
Telgarsky, Izmailov, "Understanding Reasoning from Pretraining to
Post-Training", 2026. All checkpoints/data evaluated here are the authors'
release.

	---
	license: mit
	tags:
	- ml-intern
	- replication
	- chess
	- scaling-laws
	- reinforcement-learning
	---

	[![Built with ML Intern](https://huggingface.co/datasets/huggingface/badges/resolve/main/built-with-ml-intern-sm.svg)](https://hf.co/chat?mode=ml-intern)

	# Replication: "Understanding Reasoning from Pretraining to Post-Training"

	Reduced-scale replication of core claims from **"Understanding Reasoning from
	Pretraining to Post-Training"** (Shen et al., arXiv:[2607.16097](https://arxiv.org/abs/2607.16097)),
	using the authors' released checkpoints, benchmark and code
	([pavelslab-nyu](https://huggingface.co/pavelslab-nyu),
	[Pre2Post-Chess-RL](https://huggingface.co/Pre2Post-Chess-RL),
	[GitHub](https://github.com/pavelslab-nyu/pre2post-chess)).

	Scope (agreed with the task owner): T0 = rebuild + calibrate the eval
	harness against the authors' protocol; T2 = replicate the joint pretraining–RL
	scaling law (their Fig. 3); T4 = replicate the move-level mechanism analysis
	(their Sec. 4.1 / App. H). Faithful but reduced-scale; no training of our own.

	## T0 — Eval harness (calibrated)

	We reconstructed the authors' exact evaluation protocol from their released
	code (verl fork rollout worker, `reward_function_multiturn.py`,
	`sft/evaluation/multiturn_puzzle_evaluator.py`):

	- SFT protocol (`code/eval_chess.py --protocol sft`): natural-CoT
	generation up to 1024 tokens from `{pgn}<T>`, stopping at `</T>`; then a
	move loop (≤32 tokens per move, stop at `<call_env>`), env replies injected
	after `<call_env>`, ≤5 solver moves, temp 1.0. Episode success = every
	solver move matches the ground-truth UCI line (= paper's pass@1).
	- verl protocol (`--protocol verl`, for RL checkpoints): fixed 1024-token
	thinking budget where a premature `</T>` is replaced by `<sep>` and thinking
	continues; forced `</T>` at budget exhaustion; answer phase (≤1536 tokens,
	≤6 env calls); extraction = first LAN move after `</T>`, else last LAN move
	in the segment (the authors' fallback).
	- Batched generation uses left padding (verified exactly equal to
	unbatched greedy generation); right padding was verified incorrect.

	Calibration on released checkpoints (B1+B2, 25/bin, k=8, temp 1.0):

	\| checkpoint \| protocol \| pass@1 \| pass@8 \| first-move acc \|
	\|---\|---\|---\|---\|---\|
	\| SFT `model_20m_5.3B` \| sft \| 1.5% \| 8% \| 5.3% \|
	\| SFT `model_680m_16B` \| sft \| 2.5% \| 12% \| 15.3% \|
	\| RL `model_20m_5.3B` @ step 5000 \| verl \| 3.3% \| 12% \| — \|

	This already reproduces three qualitative claims: RL improves pass@1 without
	improving pass@k; larger pretraining improves move quality; absolute pass@1 is
	percent-level, consistent with the paper's own R₀(L) = 14.62·10^(−4.30·L) fit.
	Dominant failure mode at 20M: illegal committed moves (~78%), matching the
	authors' own `illegal_move` failure category.

	## T2 — Joint pretraining–RL scaling law

	Data. 48 RL evals across the full 20M family (10 pretraining budgets
	× up to 5 RL steps; steps 100–5000) on the paper's fitting bins B3+B4
	(`results/t2/`), plus a focused high-power sweep on B1+B2 (6 pretraining
	levels × 3 RL steps, 640 draws/point; `results/t2b_*.json`). Pretraining
	validation loss L(N,T) computed on 3000 held-out Lichess 2023-01 games
	(460k tokens per checkpoint; `results/loss/`) — a proxy for the authors'
	unreleased val split.

	Finding 1 (B3+B4 floors out). On the paper's fitting bins, the entire 20M
	family measures 0–1% pass@1 (B4 = 0.000 in all 48 evals; only 40B@step4900
	reaches 1%). At our measurement scale (400 draws/point vs the paper's ~8900)
	these bins cannot resolve the correlation. The paper used B3–B4 to avoid
	saturation of larger models; at 20M with our draw budget nothing saturates,
	so we moved the high-power sweep to B1+B2.

	**Finding 2 (claim 4a — pretraining loss predicts post-RL pass@1: reproduced
	directionally).** On B1+B2, measured pass@1 at fixed RL compute (step 5000)
	vs our L: Spearman ρ = −0.54, Pearson r = −0.63 (n = 6; lower pretraining
	loss → higher post-RL pass@1). The paper reports ρ = −0.93…−0.99 via R_ref
	extrapolated to C_ref = 10²⁰ FLOPs; our extrapolated R_ref is noise-dominated
	(ρ = +0.60, wrong sign) because each per-run slope is fit from 3 points with
	±0.7% per-point noise and then extrapolated ~3.5 decades. We therefore treat
	the non-extrapolated correlation as our replication of 4a and report the
	extrapolation failure as a scale limitation.

	Measured points (B1+B2, step 5000):

	\| pretrain tokens \| L (ours) \| pass@1 \|
	\|---\|---\|---\|
	\| 0.53B \| 0.704 \| 2.0% \|
	\| 1.6B \| 0.588 \| 3.3% \|
	\| 5.3B \| 0.531 \| 2.5% \|
	\| 11B \| 0.513 \| 3.6% \|
	\| 32B \| 0.488 \| 4.4% \|
	\| 53B \| 0.480 \| 2.8% \|

	**Finding 3 (claim 4b — RL slope grows with log pretraining tokens: not
	resolvable).** Per-run slopes B from 3-point curves at our noise level are
	unidentified (Pearson r(B, log T) = −0.66, wrong sign, driven by one noisy
	point). The paper's r = +0.84 over 36 runs with ~8900 draws/point is outside
	what this budget can resolve.

	## T4 — Mechanism analysis (RL policy evolution)

	Induced root-conditioned move policies π̂(a\|s) via K=10–12 verl-protocol
	trace rollouts per puzzle and teacher-forced move scoring (paper: K=128),
	12 puzzles each from B1 (easy), B4, B5 (hard); SFT vs RL steps 100/300/500;
	Table-13 categorization (top-k=3, ε_tail=0.05). Counts per bin
	(`results/t4_mechanism.json`):

	\| category \| B1 (rl100/300/500) \| B4 \| B5 \|
	\|---\|---\|---\|---\|
	\| gt_amplification \| 1/2/2 \| 4/3/4 \| 2/3/3 \|
	\| tail_discovery \| 3/1/4 \| 0/2/0 \| 2/2/0 \|
	\| gt_regression \| 1/2/1 \| 0/1/1 \| 0/1/3 \|
	\| topk_correction \| 1/1/1 \| 0/0/1 \| 0/0/1 \|
	\| wrong_mode_amplification \| 0/1/0 \| 2/1/3 \| 2/1/1 \|
	\| other \| 6/5/4 \| 6/5/3 \| 6/5/5 \|

	Partially reproduced / not resolved. All five categories of the authors'
	taxonomy occur, including tail discovery on hard bins at intermediate RL
	steps (2/12 on B4 at step 300; 2/12 on B5 at steps 100–300). But the paper's
	headline contrast (amplification concentrated on easy puzzles, discovery on
	hard ones) is not resolved at K≈12 rollouts and 12 puzzles/bin: our dominant
	consistent signal is amplification on B4/B5, and single-count swings dominate.
	K=128 and larger puzzle samples would be needed for a decisive test.

	## Deviations from the paper

	1. Validation loss is a proxy (held-out Lichess 2023-01 games, our
	tokenization/windows) — absolute L values are not comparable to the
	authors'; correlations use our internally consistent L.
	2. Measurement scale: 400–640 draws/point vs the paper's ~8900; K≈12
	rollouts vs 128 for T4. This is the dominant limitation and is the
	explanation we propose for the un-resolved claims, since the harness
	itself is calibrated against the authors' code paths.
	3. Bin substitution for the high-power sweep (B1+B2 instead of B3+B4),
	justified above.
	4. 20m_21B/40B RL runs excluded from loss correlations (no released
	pretrain checkpoint for those budgets).
	5. RL-compute C per step estimated as 10·N·2048·(L_prompt+L_resp) with
	measured prompt length and assumed response length (paper App. D);
	slopes are unaffected by the constant.

	## Artifacts

	- `code/` — eval harness, val-loss computation, scaling-law fit, mechanism analysis
	- `results/t2/` — 48 B3+B4 RL evals + B1+B2 evals (`t2b_*` tags)
	- `results/loss/` — held-out pretraining loss for 32 checkpoints
	- `results/fit_results.json` — all fit statistics
	- `results/t4_mechanism.json` — induced policies + category counts
	- Calibration JSONs: `results/t2/…` (see T0 table; B1+B2 25/bin runs)

	## Citation

	Paper: https://arxiv.org/abs/2607.16097 — Shen, Li, Rahman, Sun, Goldblum,
	Telgarsky, Izmailov, "Understanding Reasoning from Pretraining to
	Post-Training", 2026. All checkpoints/data evaluated here are the authors'
	release.