Publish LoopBench v0.1.0 evidence bundle

CITATION.cff

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+cff-version: 1.2.0
+message: "If you use LoopBench, please cite it using this metadata."
+title: "LoopBench: Length Generalization in Looped Transformers"
+type: software
+authors:
+  - family-names: Smirnov
+    given-names: Vadim
+    email: ukint-vs@proton.me
+version: 0.1.0
+license: Apache-2.0

DYCK_REPLICATION_PLAN.md

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+# Dyck-1 independent replication protocol
+
+Locked before training at **2026-07-21T14:32:51+04:00**.
+
+## Motivation
+
+The discovery cohort (seeds 0–14) found a large far-OOD exact-match gain for
+`p=.5` over `p=0`, but the primary paired test was marginal (`t=2.247`,
+two-sided threshold `2.145`) and its balanced-accuracy sensitivity check did not
+clear the same threshold (`t=2.127`). Because the decision to collect more seeds
+followed that result, a pooled 30-seed test would inherit optional-stopping bias.
+Seeds 15–29 are therefore a separate confirmatory replication cohort.
+
+## Frozen experiment
+
+- Task: Dyck-1.
+- Arms: `p=0` and `p=.5`.
+- Training seeds: 15–29, paired across arms; no overlap with discovery seeds.
+- Six isolated five-seed jobs: seed starts 15, 20, and 25 for each arm.
+- Configuration: exactly `scripts/dyck1_seedscale.py::job_config` — two physical
+  LoopDeepNorm blocks, `R=8`, recall-add, fixed schedule, `n_ref=max`, batch 128,
+  AdamW LR `3e-4`, Muon LR `.01`, 2,500 maximum steps, curriculum enabled,
+  truncated-BPTT window `k=8`, and MPS/bfloat16.
+- Checkpoint selection: best ID validation accuracy using seed 4242, unchanged
+  from Stage 1a.
+- Held-out evaluation: 2,048 shared examples per bucket, evaluation seed
+  20260721 (bucket-specific offset as implemented), inference `R=8`.
+- All 30 runs will be trained and reported regardless of interim outcomes.
+
+## Confirmatory endpoint
+
+The sole confirmatory endpoint is per-seed far-OOD exact-match accuracy on
+lengths 62–80. For each seed, compute `p=.5 - p=0`, then apply a paired,
+two-sided t-test across replication seeds 15–29 (`n=15`, `df=14`, `alpha=.05`,
+critical `|t|=2.1447867`). Replication succeeds only if the mean difference is
+positive and `t > 2.1447867`.
+
+The replication means, mean paired difference, paired t-statistic, and decision
+will be reported regardless of direction. No task, bucket, metric, seed, or
+checkpoint will be excluded after training except a documented technical failure
+that prevents a checkpoint from being produced.
+
+## Secondary and descriptive analyses
+
+- Far-OOD balanced exact match on the same replication cohort.
+- Near-OOD (22–40), mid-OOD (42–60), and ID (2–20) exact match.
+- Discovery (seeds 0–14) and replication (seeds 15–29) results side by side.
+- Pooled 30-seed mean differences and 95% confidence intervals as descriptive
+  estimates only; no pooled confirmatory p-value.
+
+Any analysis not listed above is exploratory and will be labeled as such.

LICENSE

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README.md

@@ -0,0 +1,149 @@
+# LoopBench
+
+A length-generalization study of **looped transformers** on algorithmic tasks,
+run entirely on a single Apple Silicon machine (M4 Max, PyTorch/MPS). Tiny
+decoder-only models (~0.8–3M params) are trained on seeded algorithmic
+generators and evaluated for out-of-distribution (OOD) length extrapolation.
+
+The confirmed R=8 result: **the depth-scaling exponent `p` improves held-out
+Dyck-1 length extrapolation without materially changing ID accuracy**. An
+independent, predeclared 15-pair replication improved far-OOD exact match from
+.403 to .614 (+.211, paired t=2.734, 95% CI [.046, .377]); its class-balanced
+sensitivity check also replicated. Addition remains at 0% OOD and parity
+returns to chance despite better ID training. The completed five-task R=8 sweep
+also finds that p=.5 strongly improves prefix-sum ID trainability (.649→.953;
+exploratory paired t=2.816) and removes a copy seed failure, but both tasks stay
+at effectively 0% OOD: better optimization is not algorithmic extrapolation.
+An exploratory inference-depth probe finds that the Dyck advantage is already
+present at R=1 and peaks at R=4, so it does not support a simple mechanism where
+`p` merely prevents degradation in later loop iterations.
+
+## Method in one screen
+
+- **Model** (`loopbench/model.py`): decoder-only, RMSNorm, RoPE (base 10000),
+  SwiGLU. Two block styles:
+  - `preln` — standard pre-norm residual block (the control).
+  - `loopdeepnorm` — [DeepLoop's](https://arxiv.org/abs/2607.13491) hybrid
+    sandwich, `α = (2N)^p` on the residual, `β = (8N)^(−p)` applied once at
+    init to the output projections, `N = K · R_ref`. `p = 0` ⇒ `α = β = 1`
+    (unscaled).
+- **Loop**: `K` physical blocks applied `R` times; optional Bansal-style input
+  injection (`recall = add`). Truncated backprop keeps grad for the last
+  `backprop_window = 8` iterations. This gives full gradient coverage at R=8;
+  fixed k=8 is **not** comparable at larger R.
+- **Schedules** (`loopbench/schedules.py`): `fixed`, `uniform`,
+  `poisson_lognormal`; `n_ref ∈ {max, mean, per_batch}` sets the `N` behind
+  `α/β` (research question RQ2).
+- **Tasks** (`loopbench/tasks/`): binary addition, parity, copy, Dyck-1,
+  prefix-sums (mod 7). Pure-Python, seeded, emitting `[runs, batch, seq]`
+  tensors directly. **Full-answer prediction (FAP)**: the model reads
+  `<question> EOQ` and predicts the whole `<answer> EOS`; loss is masked to the
+  answer span; the metric is exact match over that span.
+
+## Throughput levers (built in from day one)
+
+Tiny models on MPS are overhead-bound, so the grid's wall-clock is attacked by:
+
+1. **Run-stacking** (`loopbench/stacking.py`) — all seeds of a cell train as one
+   `vmap`-ed model (`stack_module_state` + `functional_call` + `vmap`). One
+   process, N runs, ~one run's wall time. bf16 is applied by explicit casting,
+   not `torch.autocast` (which does not compose under `vmap` on MPS).
+   Memory-heavy copy/prefix cells use deterministic seed shards `(0,1)`, `(2,3)`,
+   `(4)` and merge their logs; this changes parallelism, not experiment factors.
+2. **No hidden syncs** — metrics accumulate on-device; host transfer every
+   `log_every` steps; divergence is a device-side check.
+3. **Truncated backprop** through the loop (in the model).
+4. **Early stopping** with a token ledger.
+5. **On-device pregenerated data** (`loopbench/data.py`) — one pool tensor,
+   moved to the device once, indexed per step. No DataLoader.
+
+Per-run divergence is masked out so one diverging seed cannot poison its
+stack-mates.
+
+## Quickstart
+
+```bash
+uv sync --frozen
+uv run pytest                     # unit tests (tasks, model, stacking, schedules)
+
+# Stage 0 bring-up + divergence probe (the gate before the grid)
+uv run python scripts/stage0.py
+
+# A single stacked job
+uv run python -m loopbench.train --task addition --seeds 0,1,2,3,4 \
+    --k-layers 2 --R 8 --recall add --device mps
+
+# Rebuild the committed Stage-1a summary and hero figure
+uv run python scripts/analyze_stage1a.py
+
+# Rebuild the exploratory Dyck inference-depth probe
+uv run python scripts/analyze_iteration_dynamics.py
+```
+
+Outputs: per-job JSON in `runs/<name>.json` (config, per-seed training curves,
+ID/OOD exact-match by eval length × inference-R, per-iteration activation norms,
+per-block grad norms, divergence flags, token ledger, tokens/sec) and per-seed
+checkpoints in `checkpoints/<name>/seed_<s>.pt` for full reevaluation.
+The committed CSV/JSON/SVG evidence can be regenerated without the raw training
+runs. Full reevaluation requires the separately distributed checkpoint bundle.
+
+## Comparability pins (read this before comparing numbers)
+
+Results here are **internally comparable at R=8 and only qualitatively comparable
+to prior papers**. The pins for the confirmed R=8 study are:
+
+- **Tokenizer**: task-specific symbol vocabularies (< 50 symbols), shared
+  special tokens (`PAD=0`, `EOS=1`, `EOQ=2`).
+- **Supervision**: full-answer prediction (FAP), matching Fan et al. Next-token
+  variants are out of scope.
+- **Positions**: RoPE, base 10000 (NoPE available as a flag but PE ablations are
+  out of scope).
+- **Optimizer**: Muon on attention/MLP matrices (muon_lr 0.01) + AdamW
+  β=(0.9, 0.95), lr 3e-4 on embeddings/head/norms; cosine schedule, warmup, and
+  grad clip 1.0. These LoopDeepNorm values were frozen for Stage 1a. Embeddings
+  use init std 0.02 to remove the cold-start logit spike.
+- **Precision**: bf16 on MPS (fp32 fallback off-device). Seeds control
+  data + init; run-level numeric noise on MPS is reported as part of the
+  seed variance.
+- **Checkpoint/evaluation**: weights are selected only by ID validation seed
+  4242, then reloaded and evaluated on shared held-out seed 20260721.
+- **Causal scope**: `p` changes residual scaling and output-projection
+  initialization together. Without a non-recurrent model trained under the same
+  α/β values, the Dyck result is not evidence that the benefit is specific to
+  weight tying or recurrence.
+- **Gradient coverage**: k=8 covers all R=8 iterations. The aborted R=32 gate had
+  only 25% coverage, so it is documented as a blocked method extension rather
+  than evidence about high-recurrence capacity.
+
+## What this contributes
+
+- A small Apple-Silicon research harness for stacked independent runs,
+  per-seed early stopping, best-checkpoint capture, and memory-safe evaluation.
+- A reproducible separation between improved ID optimization and genuine length
+  extrapolation across five tasks, with checkpoint hashes and generated evidence
+  artifacts. Prefix-sum is the sharp negative control: large ID gain, zero OOD.
+- A methodological warning for recurrent-depth studies: fixed truncated-BPTT
+  windows change credit coverage as R changes.
+- A bounded practical result: a separate one-seed HDFS short-to-long anomaly
+  gate did not validate a loop-model advantage; the matched Transformer won on
+  far-OOD AUPRC (.699 versus .509), so the transfer study stopped at its gate.
+
+Stage 1a is consolidated in [STAGE1A_RESULTS.md](STAGE1A_RESULTS.md). The R=32
+extension is deferred until k/R gradient comparability is solved.
+
+## Documentation
+
+- [STAGE1A_RESULTS.md](STAGE1A_RESULTS.md) — final metrics, statistical tests,
+  limitations, and evidence inventory.
+- [DYCK_REPLICATION_PLAN.md](DYCK_REPLICATION_PLAN.md) — frozen independent
+  replication protocol, committed before seeds 15–29 were trained.
+- [RESEARCH_NOTES.md](RESEARCH_NOTES.md) — RASP-L framing and practical-transfer
+  rationale.
+- [STAGE1_PLAN.md](STAGE1_PLAN.md) — frozen experiment contract.
+
+## Citation / license / contact
+
+Citation metadata is in [CITATION.cff](CITATION.cff).
+LoopBench is available under the [Apache License 2.0](LICENSE).
+
+Vadim Smirnov · `ukint-vs@proton.me`

STAGE1A_RESULTS.md

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+# Stage 1a results — depth scaling and length extrapolation
+
+## Setup and final evaluation
+
+Training swept `p ∈ {0, 0.25, 0.5}` over addition, Dyck-1, parity, copy, and
+prefix-sum with five seeds, R=8, K=2, fixed schedule, additive recall, and the
+retuned LoopDeepNorm optimizer settings. Dyck-1 p∈{0,0.5} uses a 15-pair
+discovery cohort (seeds 0–14) and a separately predeclared 15-pair replication
+cohort (seeds 15–29). Copy and prefix-sum were the completed R=8 remaining-task
+expansion; their memory-heavy cells were split into seed shards, which changes
+only execution parallelism, then merged into the canonical five-seed logs.
+
+The final numbers below do **not** select a logged evaluation step. Each saved
+best-ID checkpoint (selected on deterministic validation seed 4242) was loaded
+and evaluated on a new shared held-out set: seed 20260721, 2,048 examples per
+ID/OOD bucket, inference R=8. See `scripts/analyze_stage1a.py` and
+`artifacts/stage1a_summary.json`.
+
+| task | p | seeds | held-out ID | OOD by increasing length bucket |
+|---|---:|---:|---:|---|
+| addition | 0 | 5 | .827 | .000 / .000 / .000 |
+| addition | .25 | 5 | .945 | .000 / .000 / .000 |
+| addition | .5 | 5 | .998 | .000 / .000 / .000 |
+| Dyck-1 | 0 | 30 | .923 | .706 / .497 / .412 |
+| Dyck-1 | .25 | 5 | .929 | .790 / .683 / .557 |
+| Dyck-1 | .5 | 30 | .942 | .816 / .708 / .613 |
+| parity | 0 | 5 | .524 | .502 / .486 / .395 / .378 |
+| parity | .25 | 5 | .567 | .500 / .499 / .485 / .478 |
+| parity | .5 | 5 | .883 | .507 / .503 / .493 / .498 |
+| copy | 0 | 5 | .847 | .000 / .000 / .000 |
+| copy | .25 | 5 | .996 | .0002 / .000 / .000 |
+| copy | .5 | 5 | .996 | .0009 / .000 / .000 |
+| prefix-sum | 0 | 5 | .649 | .000 / .000 / .000 |
+| prefix-sum | .25 | 5 | .769 | .000 / .000 / .000 |
+| prefix-sum | .5 | 5 | .953 | .000 / .000 / .000 |
+
+## Findings
+
+1. **The mean ID direction is consistent across all five tasks, but the
+   strength of evidence varies.** Nominal paired tests clear the two-sided .05
+   threshold only for parity (t=7.56) and prefix-sum (t=2.82); addition
+   (t=1.72) and copy (t=1.05) have large mean gains driven by seed failures,
+   while Dyck-1 ID is nearly unchanged (.923→.942). These task-wise ID tests
+   are exploratory and not multiplicity-corrected.
+2. **ID improvement does not imply length extrapolation.** Addition remains at
+   zero OOD exact match, parity approaches chance, and both multi-token copy and
+   prefix-sum remain effectively zero across every OOD bucket even at p=.5.
+3. **Dyck-1 is the positive result.** With ID held effectively constant, p=.5
+   improves OOD exact match, and the gain is larger away from the training
+   range.
+
+## Exploratory trainability expansion
+
+These comparisons were added after the three-task core and are exploratory,
+with no multiple-comparison correction. On the fresh held-out ID set,
+prefix-sum p=.5 improves exact match from .649±.187 to .953±.103 (+.304; five
+paired seeds, t=2.816, df=4; nominal two-sided threshold 2.776). Copy improves
+from .847±.318 to .996±.006 because p>0 removes a p=0 seed failure, but the
+paired statistic is not significant (t=1.050). The substantive conclusion is
+trainability/stability, not length generalization: prefix-sum OOD is exactly
+zero, and copy has only near-bucket traces below .001 before returning to zero.
+
+## Dyck-1 discovery and pre-specified replication
+
+Both cohorts use the paired p=0 versus p=.5 comparison on the far OOD bucket
+(62–80), with training seed as the pairing unit. The first five pairs suggested
+an underpowered effect, after which seeds 5–14 were added; seeds 0–14 are
+therefore an adaptive discovery cohort, not a clean confirmatory test. After
+observing that cohort's marginal result, the replication protocol was committed
+before training seeds 15–29; see
+`DYCK_REPLICATION_PLAN.md`. Each cohort uses a two-sided α=.05 critical value
+of |t|>2.145 at df=14.
+
+### Discovery cohort (seeds 0–14)
+
+| bucket | p=0 | p=.5 | paired diff | paired t | role |
+|---|---:|---:|---:|---:|---|
+| near 22–40 | .735 | .832 | +.096 | 1.852 | secondary |
+| mid 42–60 | .536 | .725 | +.189 | 2.626 | secondary |
+| **far 62–80** | **.422** | **.613** | **+.191** | **2.247** | **discovery; nominal** |
+
+The discovery far-OOD difference has a 95% CI of [.009, .373]. Its balanced
+far-OOD sensitivity result is .437→.618 (+.182, t=2.127), just below the same
+critical threshold. The earlier `t=2.56` was a legacy estimate reconstructed
+from logged evaluations and is not a headline statistic.
+
+### Independent replication cohort (seeds 15–29)
+
+| bucket | p=0 | p=.5 | paired diff | paired t | 95% CI for diff |
+|---|---:|---:|---:|---:|---:|
+| ID 2–20 | .920 | .951 | +.031 | 1.561 | [-.012, .074] |
+| near 22–40 | .676 | .800 | +.124 | 2.472 | [.016, .231] |
+| mid 42–60 | .458 | .691 | +.233 | 3.439 | [.088, .378] |
+| **far 62–80** | **.403** | **.614** | **+.211** | **2.734** | **[.046, .377]** |
+
+The sole confirmatory endpoint replicates: the far-OOD mean difference is
+positive and its paired statistic exceeds the frozen threshold. The
+predeclared balanced sensitivity also replicates (.407→.622, +.215, t=2.853,
+95% CI [.053, .377]). Thus the result no longer depends on ordinary rather than
+class-balanced exact match.
+
+Pooling the cohorts only to estimate magnitude gives far-OOD .412→.613, a
++.201 paired difference with 95% CI [.086, .316]. No pooled confirmatory
+p-value is reported because adding seeds was decided after seeing the discovery
+result.
+
+All six replication jobs exited successfully and recorded no divergent runs,
+but emitted late, non-fatal MPS command-buffer memory warnings. This technical
+anomaly was resolved at the evidence gate rather than ignored: all 30 selected
+replication checkpoints reloaded in a fresh process, all recomputed metrics are
+finite, and every archived checkpoint hash matches the evidence CSV. The
+reported results use only those fresh checkpoint evaluations.
+
+## Interpretation and limits
+
+- The predeclared 15-pair replication, consistent with the adaptive discovery
+  cohort, supports a narrow claim: in this R=8 setup, depth scaling improves
+  Dyck-1 length extrapolation without materially changing ID accuracy.
+- The study does not establish that the benefit is specific to weight tying or
+  recurrence. The p=.5 α/β scheme is also an optimization/initialization change,
+  and there is no non-recurrent model trained with the same fixed scaling. The
+  R=1 probe still uses checkpoints trained at R=8, so it cannot fill that role.
+- On copy and prefix-sum, p improves optimization robustness but does not rescue
+  multi-token length extrapolation. It also does not rescue arithmetic or
+  parity, nor show that the effect generalizes to arbitrary recurrent depth.
+- R=32 under fixed k=8 is not comparable to R=8 because gradient coverage falls
+  from 100% to 25%. Truncated credit assignment is the leading explanation for
+  the failed R=32 gate, but k=16 did not establish causality.
+
+## Exploratory iteration-dynamics probe
+
+We tested one cheap mechanism hypothesis using the original 30 saved Dyck-1
+discovery checkpoints:
+if `p=.5` mainly stabilizes repeated computation, its advantage should grow
+as inference recurrence increases. The same 512 held-out far-OOD examples were
+evaluated at `R ∈ {1,2,4,8}` for all 15 paired seeds. The predeclared exploratory
+threshold was at least 0.10 growth in the paired p-effect from R=1 to R=8.
+
+| inference R | p=0 | p=.5 | paired difference | paired t |
+|---:|---:|---:|---:|---:|
+| 1 | .165 | .337 | +.172 | 1.744 |
+| 2 | .074 | .366 | +.292 | 3.208 |
+| 4 | .168 | .521 | +.352 | 3.942 |
+| 8 | .417 | .610 | +.192 | 2.296 |
+
+The hypothesis fails: effect growth from R=1 to R=8 is only +.021, and the
+largest separation occurs at R=4. Thus the current evidence does not support a
+simple "p prevents degradation in later iterations" mechanism. The advantage
+already present at R=1 instead points to changed training dynamics or a changed
+learned representation. This is post-hoc mechanism evidence, not a new
+confirmatory endpoint.
+
+There is a narrower post-hoc pattern: the p=.5 cohort mean rises monotonically
+with inference R, while the p=0 mean does not. That is not evidence of greater
+per-seed stability: only 8/15 p=.5 seeds are individually monotonic versus 6/15
+at p=0, and p=.5 has higher across-seed SD at every tested R. It is a useful
+hypothesis for a dedicated control, not a rescued mechanism claim.
+
+The originally logged diagnostics cannot resolve that distinction: activation
+RMS was measured after post-normalization and is mechanically about 1, while
+block-gradient norms were measured after global clipping and therefore censor
+absolute scale. A future causal run would need pre-normalization residual ratios
+and pre-clip gradient norms, but no such run is justified by the current gate.
+
+## Evidence artifacts
+
+- `artifacts/stage1a_metrics.csv` — per-checkpoint metrics and SHA-256 hashes;
+  all 125 checkpoint hashes were independently verified (125/125 matches).
+- `artifacts/stage1a_summary.json` — evaluation contract and aggregate tests.
+- `artifacts/stage1a_hero.svg` — OOD versus p, mean±SD by task and bucket.
+- `artifacts/dyck1_iteration_dynamics.{csv,json}` — exploratory inference-R
+  probe over the 30 saved Dyck-1 checkpoints.
+
+Regenerate the summary and figure with `uv run python scripts/analyze_stage1a.py`.
+With the separately distributed checkpoint bundle present, rebuild all metrics
+with `uv run python scripts/analyze_stage1a.py --reevaluate`.
+Regenerate the iteration probe with
+`uv run python scripts/analyze_iteration_dynamics.py`.

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