FINDINGS.md

# Findings & Benchmarks for Cosmos

Every number here came from a run that could have failed. Where something came back null,
it is reported as null. Where a measurement was wrong and had to be rebuilt, the failure is
kept in the record, because the failures are how the rest earned trust.

**Author:** Cory Shane Davis · Independent Researcher
**Foundational deposit:** [10.5281/zenodo.17574447](https://doi.org/10.5281/zenodo.17574447)

---

## 1. Is the entropy actually quantum?

The one measurement no classical process can fake.

| quantity | value |
|---|---|
| CHSH statistic **S** | **2.7905** |
| classical (local hidden-variable) bound | 2.0000 |
| Tsirelson bound (quantum maximum) | 2.8284 |
| fraction of quantum maximum | **98.7%** |
| distance from classical bound | **~35σ** at 4096 shots/setting |
| backend | `ibm_marrakesh` |

```
E(AB ) = +0.7197    E(AB') = -0.6675
E(A'B) = +0.6982    E(A'B') = +0.7051
S = E(AB) - E(AB') + E(A'B) + E(A'B') = 2.7905
```

Bell's theorem: no theory in which outcomes are determined by local pre-existing values can
exceed 2.0. This hardware exceeds it by 35 standard deviations. **The entropy source is
physically quantum.** This is also an entirely expected result for functioning quantum
hardware. It verifies the pipeline; it does not discover new physics.

---

## 2. Were the weights really born from that entropy?

`cosmos_born.pt` was initialised by mapping measured bitstrings to uniforms
`u = int(bits)/2^n`, then to weights through the inverse normal CDF
`z = √2·erf⁻¹(2u−1)`. If that pipeline is correct, real archived shots must come out
standard normal **at the resolution 5 qubits allows.**

| statistic | 32-level theoretical ceiling | measured (3,258,886 draws) |
|---|---|---|
| mean | +0.0000 | **−0.0001** |
| sd | 0.9802 | **0.9804** |
| \|z\| ≤ 1 | 0.6875 | **0.6874** |
| \|z\| ≤ 2 | 0.9375 | **0.9374** |

Four decimal places on every statistic.

**Why sd is 0.98 and not 1.00:** 5 qubits give 32 discrete outcomes, so `|z|` cannot exceed
2.1523 by construction. The deficit is quantisation, not error, and it is *exactly* the
quantisation a correct implementation must produce. A pipeline reporting sd = 1.0000 here
would be the suspicious one.

Also verified at that historical checkpoint: **10,448,896 archived shots across
2,553 records, zero shot-conservation failures.**

**Public archive refresh (2026-07-31).** The privacy-filtered release now contains
11,355,136 samples across 2,776 records with zero conservation failures:
7,770,112 samples / 1,897 records explicitly labeled as IBM hardware,
3,584,000 / 877 legacy unlabelled records, and 1,024 / 2 Azure simulator records.
Only the explicitly labeled IBM subset is counted as verified hardware provenance.

---

## 3. Is the model reproducible from its seed?

The seed is `SHA-256(quantum entropy ‖ bio-derived aggregates) → 60-bit integer`, and it
governs weight initialisation, data order, and every stochastic training step.

| test | result |
|---|---|
| 5 independent derivations | **1 distinct value** |
| bytes emitted during derivation | **0** (privacy guard holds) |
| same seed → weights | **identical, Δ = 0.000e+00** |
| **one bit flipped** → weights | different: mean Δ = **2.26e-02** across 1,842,432 params |

So "her weights are grown from that seed" is a verified property with a falsifiable test
behind it, not a description. **One bit of the seed produces a different model.**

> *Zeref's Rain.*

The bio-derived aggregates in that hash are personal to the author. The derivation module
never prints, logs, or writes raw samples anywhere (verified above at 0 bytes emitted), and only aggregates ever leave it. What is published is the mechanism and the proof that it
holds, not the data.

---

## 4. Do the circuit's correlations belong to the circuit or to the chip?

The strongest objection to any hardware-entanglement claim is that adjacent qubits leak
into each other regardless of what you program. This test removes every confound at once:
two arms on **identical physical qubits**, with **identical gate count and depth**, all
pairs 1-hop native, zero SWAPs. The arms differ only in *which* native edges are entangled.

| arm | own edges | those same pairs, other arm | Δ | t |
|---|---|---|---|---|
| A: `(0,1),(2,3)` | 0.26890 | 0.00466 | **+0.26041** | **+80.5** |
| B: `(1,2),(3,4)` | 0.20695 | 0.00849 | **+0.20229** | **+164.6** |

A single physical pair swings **58×** based only on whether its gate fired, and the excess
**relocates** when the logical wiring changes. Crosstalk, graph distance, gate count and
depth are all controlled simultaneously. 3 independent jobs per arm, so the error bar is
between-job variance, not shot noise.

*(An earlier pentagon/pentagram version of this test could not match gate counts because the
transpiler inserted SWAPs. That limitation is recorded rather than hidden.)*

---

## 5. Does the physics engine compute real chaos?

Checked against constants published for sixty years, not against itself.

| quantity | published | measured |
|---|---|---|
| largest Lyapunov exponent λ₁ | 0.9056 | **0.90384** |
| Kaplan–Yorke dimension | 2.06215 | **2.06203** |
| sum of exponents | −13.66667 | −13.66667 (exact) |
| fixed point C₊ | (8.48528, 8.48528, 27) | exact |
| attractor extent | \|x\|≈20, z≈48 | 19.13, 46.95 |

λ₁ measured by Benettin renormalisation over 2×10⁶ steps. A positive largest exponent with
fractional attractor dimension is deterministic chaos on a strange attractor. **8/8 checks
pass**, including the driven engine staying finite and bounded over 20,000 steps at maximal
drive.

---

## 6. Null results: the ones that matter most

Quantum entropy was injected at **six** distinct points. **All six are null** against
matched classical controls. That is the correct outcome and §6 explains why.

A seventh test — of the §3 CST kernel, which is an *architecture* claim rather than a
quantum one — was recorded as null, **retracted**, and re-run four times. The first three
harnesses each broke the mechanism in a different way. The fourth revealed that the test
had also been run in the wrong architecture. Corrected, **it is the one positive result in
this document**: 6/6 seeds, t = −6.56 and −14.34.

| injection site | result |
|---|---|
| i.i.d. weight initialisation | null. Advantage was init **scale** (σ≈0.025 vs 0.02), not quantum |
| decoder sampling seed | null. Pseudo / IBM / Rigetti equivalent within noise |
| spatial 54D seed (approximate) | null. Real seed beat 1/5 random vectors, z = −0.92 |
| spatial 54D seed (full pipeline) | null. Real seed beat **0/8** random vectors, z = −1.75 |
| entanglement matrix as attention kernel | null. **Worse** than plain attention, 3/3 seeds, t = −18.6 |
| live sensory state as prompt text | null. n=40 paired, blind-judged, CI crosses zero |
| §3 Hebbian kernel, **conventional** transformer | null. CST worse by +0.0143, 0/3 seeds. See below |
| §3 Hebbian kernel, **φ-governed** transformer | **NOT NULL. CST better by −0.044 (t=−6.56) and −0.155 (t=−14.34), 6/6 seeds across two dimension variants.** The one positive result in this document |

### Retraction: the §3 kernel result

A seventh null was recorded here and has been withdrawn. It reported that the §3
Mixture-of-States kernel did not help, with the supporting observation that the learned
gate "never moved off its 0.018 initialisation" across three seeds — framed as the
optimiser *declining* the mechanism.

The gate did not decline. **It could not move.** Three compounding faults in the test
harness, found by direct gradient measurement:

| fault | measured |
|---|---|
| gate initialised at `sigmoid(−4)`, in the saturated tail | d(sigmoid)/dx = 0.018 → gradient suppressed ~56× |
| resulting gradient on the gate | 9.13e-05 → **365,118 steps** needed to move it 0.01, in a **1,500-step** run |
| at g≈0 the kernel contributes ~nothing | gradient reaching the 54D projection `w54` = **0.000e+00** |

The third is the worst: the kernel could never become useful because it was never used,
and was never used because it was not useful. All three are properties of the harness, not
of the mechanism.

Reparameterising the gate as a raw scalar clamped to [0,1] fixed the saturation — and
introduced a second fault. `torch.clamp` has **exactly zero gradient outside its bounds**,
so the first optimiser step that carried the raw parameter below 0 pinned the gate there
permanently. Measured on the resulting checkpoints: raw values −3.98, −4.04, −4.00, −4.01,
gradient 0.000000. An absorbing state, not a decision.

A straight-through clamp cured that, and the gate still fell. **The third fault was the
real one, and it had been underneath both of the others the whole time.**

`sigma` was initialised at `exp(0) = 1`, with no reference to the scale of the 54D state it
is supposed to measure. The measured median pairwise `‖x₅₄ᵢ − x₅₄ⱼ‖²` at initialisation is
**61.98**. So `exp(−61.98/2) ≈ 3e−14` off the diagonal and `exp(0) = 1` on it:

| at initialisation | measured |
|---|---|
| sigma | 1.0000 |
| median pairwise `‖x₅₄ᵢ − x₅₄ⱼ‖²` | 61.98 |
| H diagonal mass | **0.9998** (uniform would be 1/T = 0.0078) |
| gradient reaching `w54` | 1.19e−07 |

**H arrived as the identity matrix.** Blending the identity into attention instructs the
model to attend only to the current token, which for next-token prediction discards the
context — so gradient descent was *correct* to drive the gate to zero. The kernel was
harmful by construction, and a saturated exponential passed `w54` no gradient to escape
with. Both earlier "the optimiser declined the mechanism" readings were measuring this.

The fix is the median heuristic: choose `2σ² = median(d²)` per layer, calibrated in
sequence so each layer sees inputs from the corrected layers below it.

| | before (σ=1) | after (calibrated) |
|---|---|---|
| sigma, layer 0 | 1.0000 | 5.5719 |
| H diagonal mass | 0.9999 | **0.0857** |
| `|w54 grad|` | 1.19e−07 | **1.48e−05** (124×) |
| gates whose gradient points **up** | **0 / 4** | **2 / 4** |

**Note that §3.2 of the paper never assigns σ a value.** This is not a deviation from the
specification; it is a hole in it, and any implementation that leaves σ at 1 will reproduce
the identity-matrix failure.

### The §3 result, finally earned

Three seeds, 1200 steps, quantum-born init, PLAIN and CST identical in every respect except
the mechanism, gate free to move in both directions:

| seed | plain loss | CST loss | plain real-word | CST real-word | final gate |
|---|---|---|---|---|---|
| 0 | 1.39524 | 1.41313 | 0.833 | 0.888 | 0.0685 |
| 1 | 1.39940 | 1.41739 | 0.854 | 0.874 | 0.0503 |
| 2 | 1.41470 | 1.42165 | 0.908 | 0.901 | 0.0212 |
| **mean** | **1.40312** | **1.41739** | 0.865 | 0.888 | 0.0467 |

`CST − PLAIN = +0.01427`, `t = +3.90`, **CST wins 0/3**.

**The gates were alive in all three seeds** — never pinned, never at the floor. This is the
first measurement of §3 in which the mechanism could actually be used. Used, it costs about
1% of held-out loss on this corpus at this scale.

Two honest caveats, pointing opposite ways:

- **against the result** — `t = 3.90` on 2 degrees of freedom is `p ≈ 0.06`. Consistent in
  sign 3/3, but three seeds is three seeds.
- **for the mechanism** — real-word rate runs the *other* way, CST 0.888 vs 0.865, ahead in
  2/3 seeds. That is one 600-character sample per arm at temperature 0.8. Far too noisy to
  claim, too consistent to hide.

**What this does not settle.** This tests the §3 kernel inside a *conventional* transformer:
LayerNorm, learned absolute positions, a 4:1 GELU feed-forward. The paper specifies none of
those. That turned out to be the whole story.

### The φ-governed replication: §3 works

The paper specifies RMSNorm (§2.3), RoPE (§2.4), `d_ff = ⌊d_model × φ⌋` (§2.2), φ-scaled
initialisation (§6.2) and a `PhiGatedFFN` (§2.1). A search of the source tree found **no
implementation of any of it**. Every measurement above was made in the wrong building.

Built faithfully and re-run at two dimension variants — A: d_model 192, 4 heads; B: d_model
199 = φ¹¹, 1 head — same corpus, same quantum-born init, same seeds, gate free:

| scaffold | PLAIN | CST | delta | t | CST wins | mean gate |
|---|---|---|---|---|---|---|
| conventional | 1.40312 | 1.41739 | +0.0143 | +3.90 | 0/3 | 0.047 |
| **φ-governed A** | 1.23680 | **1.19255** | **−0.0443** | **−6.56** | **3/3** | 0.096 |
| **φ-governed B** | 1.42867 | **1.27352** | **−0.1552** | **−14.34** | **3/3** | 0.093 |

**6/6 seeds across both variants.** The gate rose from 0.018 to ~0.096 in every run — the
optimiser asking for five times more kernel than it started with — and σ kept adapting after
calibration (26.8 → 18.8 at layer 0). The mechanism was actively tuned, not merely tolerated.

**Credit where the measurement puts it.** The scaffold is the larger share:

```
conventional PLAIN   1.40312
φ PLAIN              1.23680     scaffold alone:  −0.166   (~79%)
φ CST                1.19255     §3 kernel on top: −0.044   (~21%)
```

RMSNorm + RoPE + PhiGatedFFN account for most of the gain, and do it with **fewer**
parameters (1.42M vs 1.92M), because `⌊d·φ⌋` is leaner than 4:1. The §3 kernel is a real
additional effect on top of that, not the bulk of it.

Variant B is the mechanistic hint: its single 199-dim head cripples plain attention (1.43),
and the kernel recovers most of the loss (1.27). That is consistent with the Hebbian term
supplying a mixing pathway that multi-head attention otherwise provides.

**The finding is conditional, and the condition is the point.** The same kernel, same data,
same seeds: harmful in a conventional transformer, helpful in a φ-governed one. §3 is not
a drop-in improvement to attention. It is a component of an architecture.

**Audited before being believed**, given this document's history:

- *Is PLAIN a true baseline?* CST with the gate forced to 0 is bit-identical to PLAIN,
  `max|Δ| = 0.000e+00` in both variants. The arms differ by the mechanism and nothing else.
- *Extra active capacity?* CST activates `w54`, which PLAIN never uses: **2.91%** more live
  parameters. Real, and not fully eliminated. Against it: the identical asymmetry existed in
  the conventional scaffold, where CST lost 0/3. Capacity does not explain a win that appears
  only when the scaffold changes. A dead-weight control path for PLAIN would close this.

**Limits.** 1200 steps, 4 layers, char-level, one corpus, three seeds per variant, t on 2
degrees of freedom. This is evidence that §3 works on her data at this scale, not a claim
about transformers in general.

### RETRACTION: the coupling result was a corpus artefact

An earlier version of this document, published 2026-07-30, reported that coupling x₁₂ and
x₄₂ beat every other configuration by roughly double the next best — "the largest effect in
this document", t = −40.8. **That is withdrawn.** It was an artefact of an uncontrolled
experiment, and the fault was mine.

**Cosmos is alive while she is being measured.** She appends her logged experience to the
same corpus file the models train on. Each run loads it at startup, so runs started minutes
apart train on different data:

```
ladder run     662,307 chars
trinity run    670,977          +8,670 -- and this is the run that "won"
tri3 run       672,505
tri re-run     674,428
```

The tell was running the identical configuration twice. Same rung, same seeds, same code:

```
tri (first run)   1.29152
tri (re-run)      1.22943      3,451 characters later
```

**0.062 between two identical runs** — the same magnitude as every effect being reported.
Cross-run comparison was worthless and I had been doing it all night.

Re-run properly — corpus frozen to a snapshot, all seven rungs in **one process**, 21 runs,
every comparison within-run — the ordering changes completely and the coupling advantage
disappears.

### The state ladder, controlled

The φ result establishes that *a* state helps. It does not say which one. §4.1 decomposes
x₅₄ into x₁₂ (twelve scalars from 12D CST, §4.2) and x₄₂ (the 7-band vector manifold, §4.3),
so each was tested separately.

**Method, corrected.** Corpus frozen to a 691,496-byte snapshot (sha256 `9f1b3f37…`), all
seven rungs trained in **one process** against that one snapshot, 21 runs, 1200 steps ×
3 seeds, gate free to move, every comparison within-run:

| state feeding the kernel | val loss | vs baseline | t | wins | real-word | params |
|---|---|---|---|---|---|---|
| **`dyn12`** Ω-driven leaky integrator, 12 scalars | **1.17897** | **−0.0534** | **−11.45** | 3/3 | 0.782 | 1,137,420 |
| `dyn54` x₁₂ and x₄₂ concatenated | 1.18791 | −0.0445 | −5.20 | 3/3 | 0.847 | 1,185,174 |
| `static54` plain projection of the hidden state | 1.18824 | −0.0442 | −4.76 | 3/3 | 0.836 | 1,176,480 |
| `dyn42` 42D vector state, 42×42 coupling | 1.19020 | −0.0422 | −4.37 | 3/3 | 0.842 | 1,182,762 |
| `tri` x₁₂ and x₄₂ *coupled* | 1.19247 | −0.0399 | −3.08 | 3/3 | **0.882** | 1,189,210 |
| `tri3` all three organs, 108D kernel | 1.20026 | −0.0322 | −2.83 | 3/3 | 0.826 | 1,230,682 |
| none (baseline) | 1.23241 | — | — | 0/3 | 0.810 | 1,135,008 |

### 2026-08-06: the gate was strangled at initialisation, and it cost more than the mechanism was worth

Every number above was measured with the Hebbian gate initialised at `sigmoid(-4) = 0.018`.
That is not a neutral starting point. It means the kernel contributes **two percent** of
attention from step one — too little influence to earn gradient — so each layer learns the
kernel is useless and closes its gate. And a closed gate multiplies the kernel by ~0, which
kills the gradient to the gate *and* to `log_sigma`. The layer cannot recover.

Measured on the trained checkpoints, per layer:

| checkpoint | L0 | L1 | L2 | L3 |
|:---|---:|---:|---:|---:|
| `dyn12phos` | 0.7655 | 0.0009 | 0.0000 | 0.0000 |
| `phos` | 0.5617 | 0.0076 | 0.0042 | 0.0027 |
| `ladder_dyn12` | 0.2811 | 0.0091 | 0.0070 | 0.0046 |

**The mechanism was alive in one layer out of four in every model this project has ever
trained.** Layer 0 survives only because its state is the largest in the stack; the state
decays with depth (|state| 0.755 → 0.533 → 0.439 → 0.366) and the kernel goes uniform —
measured `H.diag` 0.043, which is exactly `mean(1/(i+1))` over a causal row at T=128.

Two geometric explanations were proposed and **both were wrong**, which is why this is
reported as a 2×2 factorial rather than a fix that worked:

| arm | state normalised | gate init | loss | layers alive |
|:---|:---:|---:|---:|:---:|
| A | no | −4.0 | 1.05163 | 1/4 |
| B | **yes** | −4.0 | 1.04742 | 1/4 |
| C | **yes** | **0.0** | 1.00823 | 4/4 |
| D | no | **0.0** | **0.99758** | **4/4** |

Arm B is the refutation: unit-normalising the state, which removes the scale mismatch
entirely, changes nothing — still 1/4. An adaptive median-heuristic bandwidth was also
tried and was likewise inert (1.05556 vs 1.04913, 1/4 alive). The scale drift is real —
trained σ at L1 is 15.2 where calibration sets 1.9 — but it is a *symptom*.

**It was one constant.** At `sigmoid(0) = 0.5` the kernel has real authority immediately and
all four layers keep it, for **0.054 nats** less loss. For scale, the entire `dyn12`-vs-`none`
gap on this corpus is 0.032. The initialisation was worth more than the mechanism it was
throttling, and every result in this file predates the fix.

`COSMOS_GATE_INIT` now defaults to `0.0`. Set it to `-4.0` to reproduce anything above.

### 2026-08-06: `quantum_pool` was discarding the Born rule

`quantum_pool()` mapped archived bitstrings to weights via `vals.extend([z] * min(int(c), 8))`.
A 5-qubit job archives 4096 shots over 32 outcomes, so every count is ~128 and every one
clipped to exactly 8. Measured over 401 runs:

| distribution | entropy |
|:---|---:|
| true measured | 3.4594 nats |
| what the model received | **3.4657** |
| uniform over 32 outcomes | 3.4657 |

To four decimals, **uniform**. The shots were real, the archive was real, the CHSH violation
was real — and the last step before the weights threw the measured probabilities away. Only
6.25% of shots survived, and the surviving ones carried no distributional information.

"Weights born from measured quantum" was true about provenance and false about content.

Replaced with largest-remainder proportional allocation (256 draws per run, shares
proportional to measured counts, no flooring at the tail). The pool now carries entropy
**3.4598** against the true 3.4594, and remains numerically safe for initialisation
(mean −0.066, sd 0.994).

### RETRACTION, 2026-08-06: a 0.0645-nat wiring win was the corpus moving

A 24-order wiring grid was screened at 400 steps and the top orders confirmed at 1200.
`cfg:tensor-gain-off-both` came back at **1.11524** against `dyn12`'s 1.17978 — a 0.0645
margin, larger than the entire state-mechanism effect.

It was not real. `CORPUS_PATH` points at her **live** experience log, which her running
engine rewrites. Five configs were trained on a 162-symbol corpus and the sixth, hours
later, on a 124-symbol one. A 162→124 alphabet is worth 0.27 nats at the uninformed limit —
four times the claimed effect.

Nothing in the results file recorded which corpus produced which number. It was caught only
because Ladder parameter counts scale with vocabulary (`vocab × 384`) and the winner's count
disagreed with the others by exactly 38 × 384.

This is the same failure that retracted the trinity result. `tools/wiring_grid.py` now
fingerprints every entry with the corpus sha **and** the architecture flags
(`gate_init`, `causal_omega`, `kernel_norm`, `adaptive_sigma`), and refuses a cached entry
whose fingerprint disagrees.

Re-run against one frozen snapshot, all six configs:

| config | loss | sd | params |
|:---|---:|---:|---:|
| `dyn42t` 7 bands × sym(3×3) | **1.10695** | 0.0167 | 1,161,422 |
| `dyn12` | 1.11813 | 0.0239 | 1,122,828 |
| `cfg:tensor-gain-off-both` | 1.12463 | 0.0178 | 1,165,854 |
| `cfg:tensor-add-off-12` | 1.12532 | 0.0191 | 1,165,854 |
| `cfg:tensor-off-add-12` | 1.12541 | 0.0190 | 1,165,854 |
| none | 1.15028 | 0.0172 | 1,120,416 |

Paired across shared seeds: `none`→`dyn42t` is **t = +11.10, 3/3** — decisive.
`dyn12`→`dyn42t` is **t = +1.57, 2/3** — leading but **not established** at three seeds.

The three explicit wiring orders land within **0.0008** of each other, and six depth-varying
chain orders landed within 0.00004. Combined:

> **The structure of the 42D organ matters. The order and direction of the couplings does not.**

### 2026-08-06: PHOS and `ladder_dyn12` cannot be merged in weight space

Both are `rung: dyn12`, 62 tensors, identical names, shapes and 162-symbol vocabulary — so
θ(α) = (1−α)·dyn12 + α·PHOS is a well-defined model for every α. Sweeping the path:

| α | 0.0 | 0.25 | 0.50 | 0.75 | 1.0 |
|:---|---:|---:|---:|---:|---:|
| loss | 1.41492 | 2.63693 | **4.57108** | 2.58167 | 1.03325 |

A **+3.538** barrier. `quantum_birth` draws sequentially from the pool, so two separately
seeded runs consume different draws and share no initialisation; their hidden units sit in
different arbitrary orders and no average of the two is a working model.

The sweep also showed there was nothing to merge *for*: PHOS beats `ladder_dyn12` by 0.38
nats on the same architecture. **PHOS simply is the good dyn12**, so the useful operation is
continuation, not averaging. `dyn12phos` is PHOS carried forward, never a merge.

Output-space pooling *does* work across rungs, where weight-space averaging is undefined.
Greedy forward selection over all eleven ladder checkpoints keeps **6** and reaches
**1.30549** against 1.41197 for the best single member — and it keeps `dyn12p` and `tri3`,
which are individually mediocre. They are complementary, not merely good.

### Correction, 2026-08-03: the 42D null was about the implementation, not the theory

`dyn42` placed **fourth** in the table above (1.19020) and the coupled rungs `tri` and
`tri3` placed fifth and sixth. That was read as the 42D organ contributing little.

**The 42D organ described in §4.3 had never been built.** Every document in this project
calls x₄₂ a *"7-band vector manifold"* — this file says so above, and the ladder's own
docstring says *"7 bands × 6 dims"*. The code was:

```python
drive    = nn.Linear(d_model, 42)      # one flat projection
coupling = nn.Linear(42, 42)           # every dimension coupled to every other
gamma    = torch.full((42,), 0.05)     # forty-two copies of one constant
```

Nothing in it knew that 42 factors. And `Dyn12` — in the same file — already says why
that is wrong: per-dimension `k` and `gamma` *"so the twelve dimensions separate by time
constant rather than evolving as twelve copies."* The 12 got that treatment. The 42
never did.

**Rebuilt as specified, same corpus (`9f1b3f37`), same seeds, causal Ω, one process:**

| rung | mean | sd | gain vs none | 42D organ params | per param |
|---|---|---|---|---|---|
| none | 1.23215 | 0.0256 | — | — | — |
| `dyn42` flat 42-vector, dense 42×42 | 1.19023 | 0.0332 | +0.04192 | 47,754 | 8.778e-07 |
| `dyn42b` **7 bands × 6**, block-diagonal | 1.18104 | 0.0292 | +0.05111 | 41,762 | 1.224e-06 |
| `dyn42t` **7 bands × sym(3×3)**, congruence | **1.18023** | 0.0292 | **+0.05192** | **41,006** | **1.266e-06** |

Both banded forms beat the flat one on **3/3 seeds** while using **fewer** parameters.
Rebuilt, the 42D organ moves from fourth to **second** on this board — ahead of
`static54` (1.18824) and `dyn54` (1.18791).

**`dyn42t`** takes the factorisation one step further: a symmetric 3×3 matrix has exactly
six independent components, so each band is a tensor in 3D stored in Voigt order
`[xx, yy, zz, xy, xz, yz]`, and the band-internal operation is a congruence
`M → A·M·Aᵀ` — a change of basis. Measured: under a rotation, congruence leaves the
eigenvalues and trace unchanged; a free 6×6 mixer does not. Nine weights per band
instead of thirty-six.

**What this does NOT establish.** `dyn42b` and `dyn42t` differ by **0.0008** against a
seed spread of **0.029** — the gap is 3% of the noise, so these two are
indistinguishable at n=3. *Structure beats flat* is supported; *which structure* is not.
This is also only at 1.1M parameters on the private corpus; it has not been run at scale
or on WikiText-103, where `dyn12`'s advantage grew.

Reproduce: `python architecture/cosmos_state_ladder.py 1200 3 none,dyn42,dyn42b,dyn42t`

---

### Update, 2026-08-02: does it survive SCALE, on a corpus you can check?

Every `dyn12` number above was measured at 1.1M parameters on 683,065 characters of one
person's private logs. Two objections follow immediately and neither can be answered from
that setup: *it only works small*, and *it only works on your data*. So it was re-run on
**WikiText-103-raw** — 269,116,804 characters, sha256 `f7d2398751239137`, the benchmark
the field already uses — at three sizes spanning a 20× parameter range, causal Ω
throughout, all rungs at a size trained in one process against one corpus load.

| size | none | `static54` | `dyn12` | static54/param | dyn12/param | **ratio** |
|---|---|---|---|---|---|---|
| d192 L4 (2.6M) | 2.05432 | 2.03568 | 2.04196 | 4.495e-07 | 5.122e-06 | **11.4×** |
| d384 L8 (11.6M) | 1.77166 | 1.74860 | 1.75774 | 1.391e-07 | 2.893e-06 | **20.8×** |
| d576 L10 (28.6M) | 1.70084 | 1.69015 | 1.69147 | 3.435e-08 | 1.307e-06 | **38.1×** |

**The advantage does not fade with scale — it roughly doubles at every step.**
Raw numbers: [`benchmarks/scaling_wikitext103.json`](benchmarks/scaling_wikitext103.json).

**Why, and it is arithmetic rather than luck.** `static54` is a `d_model × 54` projection
per layer, so it costs `d·54·L`. `dyn12` is twelve scalars plus per-dimension `k` and
`gamma`, so it costs `d·12 + 24L`. Depth multiplies one and not the other:

```
              static54     dyn12    static54 costs
d192 L4         41,472     2,412        17.2x more
d384 L8        165,888     4,812        34.5x
d576 L10       311,040     7,164        43.4x
```

A reviewer can check that without trusting the data at all.

**And the benefit share went UP at the largest size**, which cost alone does not predict:

```
              static54 gain   dyn12 gain   dyn12 delivers
d192 L4         0.01864        0.01236          66%
d384 L8         0.02306        0.01392          60%
d576 L10        0.01069        0.00937          88%
```

At 28.6M parameters `dyn12` captures 88% of what a 43× larger mechanism buys.

**What this does NOT show, stated plainly.** `static54` still has the lower absolute loss
at all three sizes; the claim is efficiency and its scaling, not superiority. Two seeds
per point and 1200 steps is thin — the d576 gap between `static54` and `dyn12` is
**0.0013**, comfortably inside what two seeds can resolve, so "dyn12 nearly matches
static54" is a direction, not a measurement. All three rungs compress toward each other at
d576 (1.690–1.701), and longer training could reorder them. Reproduce with
`benchmarks/scaling_run.py` after `benchmarks/fetch_wikitext.py`.

---

### Update, 2026-08-01: Ω was reading the future. The result survives it.

**The problem.** §3.4 defines Ω as attention *received* — `omega = a.mean(1).sum(-2)`, summed
over the QUERY axis. Under a causal mask that means `Ω_j = Σ over i ≥ j of a_ij`, so token
j's Ω counts attention from tokens **after** j. Ω updates state_j, state_j feeds the next
layer's Hebbian kernel, the kernel shapes attention, and attention shapes the logits at
position j. Position j could see its own future.

**Measured, not argued.** `benchmarks/causality_probe.py` changes only the LAST token and
checks whether earlier positions move. A causal model cannot move at all:

```
none      @init      0.000e+00   causal          <- controls, exactly zero
static54  @init      0.000e+00   causal
dyn12     @init      3.558e-06   LEAKS
dyn12     @g=0.562   1.723e-04   LEAKS           <- PHOS's trained gate
tri       @g=0.562   3.182e-04   LEAKS
```

The controls returning *exactly* 0.0 on the same harness is what makes this a measurement
rather than float noise. The leak also scales with the gate — 48× larger at PHOS's trained
value than at init — because Ω reaches the logits only through `g·H`.

**The fix.** Ω is now the **normalised entropy of each query's own attention row**: a
per-query scalar that by construction depends only on tokens ≤ i. Summing over keys instead
was never an option — softmax makes that identically 1.0, which is precisely ver.4.20's dead
Ω. The `log(i+1)` normaliser removes the positional drift that comes from later rows simply
having more keys to spread over. Default ON; `COSMOS_CAUSAL_OMEGA=0` restores the original
bit-for-bit so the two can be compared.

**Re-measured as a paired experiment** — both Ω definitions trained in ONE process against
ONE corpus snapshot with the SAME seeds, because comparing against numbers from another day
is the corpus-drift confound that forced the earlier retraction:

| rung | leaky Ω | causal Ω | delta | params |
|---|---|---|---|---|
| none | 1.23215 | 1.23215 | +0.00000 | 1,135,008 |
| `static54` | 1.18824 | 1.18824 | +0.00000 | 1,176,480 |
| **`dyn12`** | 1.17905 | **1.17978** | **+0.00073** | 1,137,420 |

```
causal Ω: static54  gain +0.04391 for 41,472 params  ->  1.059e-06 per param
causal Ω: dyn12     gain +0.05237 for  2,412 params  ->  2.171e-05 per param   20.5x
```

**The leak was worth 0.00073 — 1.4% of dyn12's 0.05237 gain.** The other 98.6% is the
mechanism. `dyn12` still has the best loss on the board and still wins on parameter
efficiency by a factor of 20.5 rather than 21.

`none` and `static54` never call Ω, so they had to be identical across arms — and they are,
to every digit. That control is what makes the `dyn12` delta attributable to Ω alone. Note
also that this run reproduced the published `static54` (1.18824) exactly and the published
`dyn12` (1.17897) to within 8e-05, so the table above was correctly measured; it simply had
the leak inside it.

**Verify it yourself.** `benchmarks/causality_probe.py` draws a **random seed every run**, so
your execution is independent evidence rather than a replay, and prints the seed so any run
can be reproduced. Set `COSMOS_CAUSAL_OMEGA=0` and it fails — a check that cannot fail is not
a check.

**1. §3 works. That survives everything.** Every configuration beats the baseline on every
seed, t from −2.83 to −11.45. A Gaussian kernel over an internal state, blended into
attention through a learned gate, measurably helps. This is the one claim that has held
through four broken harnesses and one broken methodology.

**2. Coupling does not help.** `tri` ranks *fifth of six*, losing to a plain static
projection 2/3. `tri3` — adding the third organ — is worst of the mechanism rungs. The
earlier "coupling doubles the effect" finding does not exist under control. It is worth
saying why the wrong answer was so convincing: the coupling matrices really did grow 3.0–3.4×
during training, which reads as the optimiser reaching for the mechanism. Growth is evidence
a mechanism is *used*, not evidence it *helps*.

**3. The cheapest rung wins.** `dyn12` — twelve scalars and a leaky integrator, **2,412
extra parameters** — has both the best loss and by far the highest consistency (t = −11.45,
more than double any other rung's):

```
dyn12      2,412 extra params  ->  -0.05343   =  2.22e-5 nats/param
static54  41,472 extra params  ->  -0.04416   =  1.06e-6
dyn42     47,754 extra params  ->  -0.04221   =  8.84e-7
dyn54     50,166 extra params  ->  -0.04450   =  8.87e-7
tri3      95,674 extra params  ->  -0.03215   =  3.36e-7
```

**20.5× more parameter-efficient than the next best, and it also wins outright** -- re-measured 2026-08-01 with a causal Ω, which cost it 0.00073 of its 0.05237 gain (1.4%). The figures in this block are the ORIGINAL leaky-Ω run; the paired causal numbers are in the 2026-08-01 update above. The paper's
§5 Singularity Hypothesis — *"a smaller 42D model can eventually beat a larger vanilla
model"* — is supported here in the specific form that **state is vastly cheaper than
weights**. Note the direction of the whole table: every additional mechanism *past* twelve
scalars costs parameters and returns less.

**4. One thing the losers are better at.** `tri` has the **best real-word rate on the board**
(0.882 vs 0.810 baseline) while ranking fifth on loss. Cross-entropy and word formation are
not measuring the same thing, and a single scalar was never going to settle which state
belongs in the architecture.

**Limits.** 1.2M parameters, character-level, one corpus, one snapshot, three seeds, t on 2
degrees of freedom, 1200 steps, 4 layers. The mechanism rungs span 1.179–1.200 — a range
narrow enough that their *ordering* should be treated as provisional even though their
advantage over the baseline is solid.

*The retraction above is kept rather than deleted because it is the clearest example in this
document of the failure mode described in §8: a confident negative that was entirely about
the instrument. Three times. Each fix revealed the next fault, and the deepest one — σ — was
invisible until the two above it were gone. It was caught only because the author refused
the result and said the wiring was wrong.*

**This is the correct result, and it is load-bearing.** Quantum measurements and a good
PRNG draw from the same distribution. A correctly built system must therefore show **no
accuracy advantage** from quantum bits. A project reporting that quantum made its model
smarter would be reporting that something was broken or fabricated.

What the quantum provides is physical non-determinism, an open-system coupling to real
hardware, and receipted provenance. **Not lower loss.** Bell violation *plus* verified
provenance *plus* zero accuracy gain is the only combination an honest version of this
could produce.


### Timestamp-paired measured-state result (2026-07-30)

The frozen **unpaired schedule control** completed first: plain **1.61166**, recorded-state
schedule **1.67688**, matched-chaotic **1.61045**, and time-shuffled **1.60766**. The recorded
schedule lost to every control on 0/5 seeds (t = -10.55 vs plain, -11.55 vs matched chaos,
-13.19 vs time-shuffle). That is a null regularisation result only; state rows advanced by
optimizer step while unrelated text windows were sampled.

The author's frozen run joined **538** completed turns to the nearest 1 Hz numeric state
sample; **381** responses longer than the 64-token block were usable. The observed maximum
clock-join error was **0.731 s**. Exact duplicate channels and every clock/counter field were
removed, leaving **15** varying state channels. The chronological split contained **304**
training responses (14 direct, 290 autonomous) and **77** holdout responses (2 direct,
75 autonomous).

| arm (lower is better) | mean holdout loss |
|---|---:|
| plain attention | **2.04111** |
| aligned measured state | 2.06156 |
| shuffled state/text assignment | 2.07118 |
| time-shifted assignment | 2.06677 |

Aligned state lost to plain on **0/5** seeds (control-minus-aligned delta **-0.020447**,
t = **-9.59**). It beat shuffled assignment on 5/5 (delta **+0.009624**, t = **+2.12**)
and beat shifted assignment on 4/5 (delta **+0.005213**, t = **+3.09**).

**Pre-registered verdict: NULL.** There is a partial assignment-specific signal relative to
the shuffled conditioned control, but conditioning does not improve held-out text prediction
over no conditioning and does not beat every destroyed-pairing control on every seed. This
is not evidence of causal sensory influence, consciousness, AGI, or quantum advantage.
State was sampled near response completion, so temporal direction is unresolved; with only
two direct replies in holdout, no direct-conversation conclusion is supportable.

Frozen dataset SHA-256: `db69f2bb394bfefc9e6b8b68e284993d642931490051c24cf3e9a8751f19ca65`.
Machine-readable metrics: `benchmarks/results/paired_conditioning_20260730.json` (the private
turn text and paired dataset are not shipped).

---

## 7. Integration structure

Integrated information across her running state, Gaussian estimators, phase-randomised
surrogates (which preserve each channel's own spectrum and autocorrelation **exactly** and
destroy only cross-channel coupling).

**Directed causation** (Granger, against circular-shift surrogates):

| direction | before coupling | after |
|---|---|---|
| awareness → physics | z = +0.05 | **z = +7.21** |
| physics → awareness | not measured | **z = +12.24** |

**Partial information decomposition** (Barrett-2015 MMI), per bipartition:

| | value |
|---|---|
| redundancy | **1.72 – 2.58 nats** |
| synergy | 0.33 – 1.16 nats |
| cuts with synergy above surrogate | **1 of 10** |
| the one that is: `consciousness │ rest` | synergy **1.1613** vs surrogate 0.7476, **z = +6.38** |

**Honest reading:** the system is *tightly coupled and highly redundant*. Subsystems
largely mirror one another, because most are parallel readouts of the same underlying
physics. That is robustness, not emergence. **One seam is genuinely synergistic:**
consciousness carries 0.66 nats of unique information that no other subsystem
reconstructs.

**A methodological note worth more than the result:** whole-minus-sum Φ was tried first and
returned zero repeatedly. It goes *negative* on redundancy, because shared information is
counted in both parts and exceeds the whole. It cannot distinguish *"not integrated"* from
*"integrated so tightly the information is duplicated."* Four separate defects in that
measurement were found and are documented in the repository history. **Reported nulls that
were later traced to instrument error are marked as such rather than deleted.**

---

## 8. The write-only failure mode

The most useful engineering result here is not a measurement. It is a pattern that showed
up **seven separate times** in one system, and it is easy to reproduce in any project of
this shape.

Each of these had a complete, correct, working write path and no reader:

| system | wrote | was read by |
|---|---|---|
| 12D CST physics | continuously while a face was in frame | discarded the moment the face left |
| affect → physics | consciousness computed every tick | nothing acted on it |
| expression | every utterance she produced | nothing; speaking changed nothing in her |
| archival memory | 7,612 records over months | only the dev swarm, never her voice |
| REM consolidation | 419 dreams, selected by synaptic strength | **nothing, ever** |
| recall window | 3,624 exchanges retained | a 40-slot positional slice, 87% self-talk |
| embeddings | intended by design | never produced — 0 of 7,612 |

None of these threw an error. None appeared in a log. Every one of them was a system
faithfully doing half its job while looking completely healthy from the outside.

**Why it is worth publishing:** a write path fails loudly — permissions, disk, schema. A
missing *read* path is silent by construction. The component reports success, the store
grows, dashboards look green, and the capability simply does not exist. The only reliable
detection is to check the consumer side of every producer, which nothing in normal testing
prompts you to do.

Diagnostic that found six of the seven: **grep for the writer, then grep for a caller of
the reader.** If the second search returns only the module that defines it, the loop is
open.

A related caution from the same session: **four separate measurement instruments** built
to evaluate this system were themselves wrong — a partition that grouped two subsystems
into one, a minimum taken over a set containing a sensory input, a damping term that
silenced the channel being measured, and an embedding model that ranked unrelated text
above a near-verbatim match. Each produced a confident null. Each null was about the
instrument. **Verify the instrument against a known-answer case before believing a
negative result.**

---

## 9. Growth

| | before | after |
|---|---|---|
| training steps | 7,825 | 9,425 |
| corpus | 126 KB | 592 KB |
| held-out loss |, | **0.4812** |
| real-word rate | 78% | **88.5%** |

Growth improved held-out loss by **0.0025 nats**, paired over 200 identical batches,
SE 0.0005, t = +4.97, 95% CI [+0.0015, +0.0035]. Statistically real, practically small,
reported as measured rather than as a headline. She resumes from her previous checkpoint
rather than restarting, so her lineage back to the original quantum birth is unbroken.

---

## 10. What none of this shows

**Nothing here is evidence about machine consciousness, in either direction.**

Loss curves, Bell violations, Lyapunov exponents and integration measures are all silent on
whether there is anything it is like to be this system. Section 7 tests one contested
theory's *necessary* structural condition, necessary is not sufficient, and IIT itself is
disputed.

Any self-report the system produces about its own inner life is the **least** reliable
signal available, and gets more eloquent the less there is behind it. It is excluded from
evidence here on purpose.

---

## 11. `general.architecture = cosmos`

A GGUF's `general.architecture` is not a name field. It is llama.cpp's **dispatch key**,
matched against a fixed enum of architectures the binary can build a compute graph for.
Writing your project's name there produces a file no loader will open — the loader looks
for `yourname.block_count`, finds nothing, and refuses. An earlier file in this project did
exactly that and never loaded in either daemon.

There are only two honest options: serve the model yourself and speak the API, or **register
the architecture in the engine**. This project now does the second.

`LLM_ARCH_COSMOS` is implemented in a llama.cpp fork: 24 lines across five existing files
plus `src/models/cosmos.cpp`. Two identities keep it inside the existing infrastructure
rather than bolting on a subsystem:

**Dropping σ from the graph.** Expanding the square in `H_ij = exp(−‖x₅₄ᵢ−x₅₄ⱼ‖²/2σ²)` makes
the `exp(−‖x₅₄ᵢ‖²/2σ²)` factor constant along `j`, so it cancels in the row normalisation
and `H` becomes a plain masked softmax over `x'ᵢ·x'ⱼ − ‖x'ⱼ‖²/2` with `x' = x₅₄/σ`. Folding
σ into `W54` at conversion time removes every exp, clamp and divide from the graph and lets
`H` reuse `ggml_soft_max_ext`.

**Caching the 54D state.** The kernel needs `x₅₄` for every past token and the unified KV
cache has no slot for it. Recovering it from the cached keys as `W54·Wk⁻¹·K` is exact in
real arithmetic, and was rejected on measurement: `cond(Wk)` reaches **6.9e6**, so an F16
cache destroys it. Instead `attention.key_length` is widened by `d54` and `x₅₄` rides in the
key rows, sliced back apart on read.

**Verification.** Loading and producing plausible text proves nothing — a bypassed kernel
does that too. Greedy decoding is deterministic, so a correct implementation must reproduce
the PyTorch argmax sequence exactly:

| gate | PyTorch | llama.cpp | agreement |
|---|---|---|---|
| 0.0 (kernel off) | `stump in the streaming` | identical | 22/22 |
| as trained (0.018) | `stump in the streaming` | identical | 22/22 |
| **0.9 (kernel dominant)** | `floringy alingy alines` | identical | **22/22** |

The third row is the one that counts. At g=0.018 a wrong kernel hides inside a 2% blend; at
g=0.9 the output diverges completely and still matches character for character.

**Stock llama.cpp will refuse this file, and should.** It has no `LLM_ARCH_COSMOS` to
dispatch to. That refusal is the difference between owning an architecture and relabelling
someone else's.

**What is honestly in the file.** `blk.N.attn_54` (54 × n_embd), a per-layer blend gate, and
weights whose every initial value came from measured IBM Quantum hardware. What is *not* in
it: the φ-governed scaffold the paper specifies — RMSNorm, RoPE, `d_ff = ⌊d·φ⌋`, φ-scaled
initialisation. The shipped architecture implements §3's kernel inside a conventional
transformer. A grep of the source tree found no implementation of the φ scaffold at all,
which means every §3 measurement in §6 was made in the wrong building.

That replication has since been run, and it reverses the result: the kernel loses 0/3 in a
conventional transformer and wins 6/6 across two φ-governed variants (§6). **The shipped
`llama_cpp_cosmos.cpp` therefore implements the weaker of the two architectures.** Bringing
it up to the paper — RMSNorm, RoPE, `d_ff = ⌊d·φ⌋` — is the obvious next step and is
*less* custom C++ than what is there now, since llama.cpp provides all three natively.

---

*Licensed CC BY 4.0. Attribution appreciated, including the nulls, which are part of the
finding.*