# 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`.