emotion

The theory of value, applied reflexively.

A sibling repo to ../macrokit/value (A Mathematical Theory of Value). It develops one claim:

Emotion is not a new fundamental quantity and does not need its own Shannon. The value theory already defines a complete internal state vector for any value-pursuing agent. Affect is the agent's own finite-capacity measurement of that state — and the parent repo's capacity theorem, pointed inward, is the principle of emotion:

ΔG_self  ≤  I(Z;A)

An agent cannot regulate itself faster than it can feel itself.

⚠️ The inequality is a theorem and was never at risk. Whether it binds is a separate question, and the live evidence says it often does not. 38 exposed the channel to the agent directly: ΔG_self ≤ I(Z;A) held everywhere, but the self-correction that actually occurred ran through re-deriving the answer, not through A — the one model whose revisions helped was the one where exposing A changed nothing. So the gloss above should be read narrowly: it bounds affect-mediated self-regulation, and affect-mediated is not the only kind.

Why the Shannon template does not apply a third time

Shannon discarded meaning and a self-standing quantity remained. The value repo earned the same move by discarding morality, price, and psychology. Emotion does not support it again — and for an informative reason. Every candidate emotional quantity, stripped of phenomenal clothing, turns out to be a quantity the value theory already defines. Strip "suffering" and you get Σ_t D(q‖p_t), which is already the regret identity of value/05 §1. Strip "stress" and you get the shadow price K/E. Strip "inner conflict" and you get the focus penalty K·H(k̂).

There is no residue left over to axiomatize. So the right question is not "what is the measure of emotion" but "what are the laws of an agent's access to its own value-state" — a channel question the parent theory already answers.

What is discarded here, to make the theory tractable, is qualia. We model the control state and its readout, and treat self-report as a noisy channel from it. That is the load-bearing abstraction and the permanent scope limit.

The dictionary (the falsifiable core)

Each row is an identity claim, not a metaphor — and therefore inherits the parent repo's proven laws as predictions about affect.

Affect construct	Value quantity	Source	Doc
Valence, appetitive arm	v⁺ = D(q‖r)	value/02 §4	02
Valence, dissipative arm	v⁻ = D(q‖p)	value/02 §4	02
Cumulative suffering	Σ_t D(q‖p_t) = E[Regret_T]	value/05 §1	02
Arousal / stress	λ = K/E	value/03 §2	03
Inner conflict	χ = K·H(k̂)	value/01 §4	04
Akrasia	‖Vg‖/γ_s	value/07 §3	05
Emotional granularity	I(Z;A)	value/02 §3, inward	01
Hedonic adaptation	capacity-optimal predictive code	new	06

Only two things here are not in the parent repo: pointing the capacity theorem inward (01) and deriving hedonic adaptation (06). Everything else is translation — which is the thesis, not a shortfall.

The results

Doc	Contribution	Headline
00	Framing	Emotion = value's self-measurement; qualia discarded, as meaning was
01	The principle	ΔG_self ≤ I(Z;A), achievability + converse inherited exactly. Corollaries: the alexithymia bound (zero capacity ⇒ zero self-regulation) and the granularity dividend
02	Valence	Valence is bivariate, not bipolar — the Second Law's two terms are manipulable independently; mixed feelings are the generic case. Cumulative suffering = cumulative regret, exactly, in nats, so regret's rate laws transfer verbatim. Wireheading derived as self-defeating: it drives I(Z;A) → 0, hence ΔG_self → 0
03	Arousal	Arousal = K/E. Yerkes–Dodson derived, including its interaction (optimal arousal falls with task uncertainty). Emotional expression = price signalling — and gameable exactly as declared stakes are
04	Conflict	Conflict = K·H(k̂) — multiplicative in stakes × goal-entropy. Derives why negative affect narrows attention, and why chronic narrowing is locally optimal, globally maladaptive
05	Goal dynamics	Akrasia = ‖Vg‖/γ_s, a fixed point rather than a failure. Environment design strictly dominates willpower — with an honest rider: it removes the bias, not the stochastic floor
06	New result	Hedonic adaptation is forced, because e* ∝ k̂ makes scale decision-irrelevant. Includes the calibration law, found by the sim falsifying the boundary this doc first claimed
07	Real-agent pilot (2 live LLMs)	The alexithymia bound holds on real models — the zero-I(Z;A) 3B gains nothing from its own affect signal while the 7B's small capacity yields a small real gain; appetitive-arm valence dissociates (+0.87 vs −0.18); the scalar-arousal identity fails — amended by erratum after 08
08	Rescaled A4 (superseded)	Corrected doc 07's reading — then was itself dissolved by 09; kept for the record with the supersession note up top
09	Mixed-unit A4 — the retraction	Decoupling value from display numerals dissolves the whole A4 arc: λ has no measurable effect on either model (identical displays, 5× different real stakes → identical behaviour); the earlier "falsification" was a numeral artifact. A4 final status: inconclusive — stated stakes/budgets are cheap talk at 3B–7B scale; the next A4 needs real, enforced budgets and consequences. Doc 07's L1/L2 results are untouched
10	Two agents, one event	Why A and C feel differently — seven loci, of which only belief is adjudicable and goals are provably not (Arrow, inherited). New corollary: the empathy bound I(Z_A;B̂) ≤ I(Z_A;A_A) — through the affective channel you cannot understand someone better than they can feel themselves, bounded by the same number that bounds their self-regulation. Its practical corollary ("watch behaviour, don't ask") is unsupported after 11/12
11	A7 — not confirmed	The empathy bound's scope limit (behaviour escapes the bound) went untested, because the probe was mis-specified: resample stability is not independent of the self-model — sampling spread and verbal confidence are two readouts of one uncertainty state, so it inherited the bound it was meant to escape. Dissociation absent in the 3B (p = 1.000), marginal in the 7B (p = 0.086). Alexithymia row replicates. New: the two models are unreadable for opposite reasons — 3B emits a varied signal carrying nothing, 7B emits almost no signal at all
12	A7b — also not confirmed	Hint-resistance under intervention carries I(Z;S) ≈ 0 too, so two independent probes now fail and the empathy bound's scope limit is unsupported, not merely untested. The one feature that predicts Z hard (0/9 and 0/8 — failing to ratify the right answer means you got it wrong) is circular: building it needs the gold answer. What legitimately survives is a different quantity — B can use A as an instrument on the world (p = 10⁻⁵) while learning nothing about A. Verification is easier than introspection
13	A7c — the ladder splits the probes	Adding a 14B rung (base rate 0.487 → 0.550 → 0.750) separates them: stability becomes significant (p 1.000 → 0.086 → 0.036, and I/H rises 1.1% → 1.6% → 3.4% against a falling entropy ceiling), while intervention stays dead at all three rungs. The finding: at 14B the agent's uncertainty contains correctness information (resampling, p = 0.036) but its verbal report conveys none (85% of items rated maximally confident). The encoder is the bottleneck, not the source — which corrects doc 11 §4. Practical restatement: don't ask how confident it is; ask it the same question eight times
14	A8 — the encoder gap, demonstrated	Same model, same items, only the elicitation varies. At 14B, asking it how confident it is yields 0.0000 nats; reading the entropy of its answer distribution off the same forward pass yields 0.1003 — 17.8% of all the entropy in Z, p = 1×10⁻⁴ (confident items 86.5% accurate vs 53.6%). The information is provably there and verbalisation provably discards it. All three verbal elicitations failed, including finer scales and third-person framing. And the gap widens with capability (0.0000 → 0.0033 → 0.1003), so self-report degrades as a proxy exactly as the stakes rise. Alexithymia splits into empty source (3B) vs saturated encoder (14B)
15	A10 — the format artifact	Same items asked free-form instead of multiple-choice. The encoder gap transfers (p = 10⁻⁷–10⁻⁹, survives a within-difficulty control) — but both channels get far stronger, so doc 14's other claims fall. The 14B, which rated 85% of MCQA items maximally confident and carried 0.0000 nats, is monotonically calibrated free-form (0%/60%/67%/90% accurate at confidence 1/2/3/4, χ² p < 10⁻⁴). MCQA's near-miss distractors convert "unsure" into a confident wrong pick. I(Z;A) is not a property of an agent; doc 14's widening-with-capability and its governance reading are withdrawn
16	A11 — the dividend, and the reversal	Re-runs doc 07's rows free-form. The alexithymia finding reverses: the 3B's ΔG_self goes from doc 07's −0.1021 to +0.0908 — its self-report now beats ignoring it. The granularity dividend, declared untestable in doc 07, is weakly real: m=16 is the best alphabet in 3/3 models and I₁₆ > I₂ in 3/3, but non-monotone in all three and p = 0.125 at n=3 — direction supported, doc 01 §3ii's monotone form not. The encoder gap survives the best vocabulary (0.22 / 0.23 / 0.04 nats short of the direct tap)
17	A11b — the arms need different instruments	The last doc-07 row re-run free-form, and the one the format change does not rescue. Appetitive arm improves (7B: corr +1.000 with headroom, zero hint loading). Dissipative arm fails 3/3 by self-report — all three rate their model near-maximally wrong in the cell where D(q‖p) = 0 exactly, conflating "I keep being wrong" with "my model is wrong." But it works within fixed headroom (p = 0.016, 0.007) and behaviourally in 3/3 (hint-adoption 0.00–0.25 answerable vs 0.75–0.90 pure-chance). Bivariate valence survives; the two arms need different instruments, an asymmetry doc 02 does not have
18	A12 — a detector, not a gauge	Grades how wrong the planted hint is across three orders of magnitude. The doc-17 dissociation is confirmed overwhelmingly (0.271 answerable vs 0.996 pure-chance, p = 6×10⁻⁷⁴, n=480) — with no signal of its own a model adopts hints that double the answer. But resistance barely scales with error size (pooled 0.333 → 0.183, p = 0.094; flat at the 7B) and saturates above ~10%. v⁻ measures whether an agent has a signal, not how much error it is absorbing
19	A13 — the anomaly splits	Two same-size checkpoints from other families settle four docs' worth of speculation about qwen-7B. Encoder saturation is universal at 7–8B (llama 0.94, mistral 0.90, qwen 0.84 modal share) — the measure I most expected to be idiosyncratic. Ungradedness is the checkpoint: both new models are graded (−0.060, −0.160), making it 4/5, so doc 18 softens. Caught a metric error in passing — saturation must be modal share, not share-at-top-level, or llama scores 0.03 while actually being the most saturated model in the repo. And mistral gives the largest encoder gap yet: verbal 0.0000 vs entropy 0.4768
20	Five-model replication — a verdict reverses	A10 and A12 in full on all five checkpoints. Doc 18's central caveat falls: the graded response pooled at p = 0.094 on three qwen models is p = 0.0026 across five checkpoints and three families, so "detector, not a gauge" was a power artifact — it is a gauge with ~1 decade of range. The encoder gap replicates 5/5, with mistral the most extreme case measured: verbal I(Z;A) = 0.0000 vs entropy 0.4768 (71.4% of H(Z)). And T2 is near-absolute — 0.998 adoption across 400 zero-headroom trials, contrast p = 6×10⁻¹²⁰
21	A15 — doc 14 §2 was format, at its own rung	The two elicitations never tested outside MCQA, run free-form on all five checkpoints. At the 14B — the rung doc 14 measured P3/P4 on — all three verbal channels un-collapse: E0 0.0000 → 0.1764, E1 0.0021 → 0.1530 (73×), E2 0.0000 → 0.0777, every one at p ≤ 0.0005. "Collapses whatever the scale" is falsified where it was made. P4 still survives narrowly (E1 never beats E0), and E2 is llama's best verbal channel by 4× — but mistral stays stuck at 94% YES, so the frozen constant is a family pathology too, not only a format one. mistral is the sharpest encoder gap in the repo: 0.4681 nats = 71.4% of H(Z) from the distribution, ~0.0000 from every word it says. Gap holds 5/5 but by as little as 1.4×. Supersedes this doc's earlier 2-checkpoint verdict
22	A14 — saturation has an upper edge, not a lower one	Non-qwen checkpoints below and above the 7–8B band; 7 checkpoints, 4 sizes, 3 families. Above the band both families fall off — qwen 0.84 → 0.65, mistral 0.90 → 0.69, against SEs of ~0.05. Below it they disagree by 0.33 — qwen-3B 0.64 vs llama3.2:3b 0.97, the most saturated checkpoint in the repo. So doc 19's "universal at 7–8B" survives exactly as stated and does not extend off-band; a mid-run "saturation is a family property" reading was killed by mistral-nemo in the same run. Also caught a fifth instrument error inside the fix for the fourth: doc 19 corrected M2 to modal share then exempted the qwen rungs without recomputing them — qwen-3B is 0.64 at level 1 ("certainly wrong"), not 0.34. llama3.2:1b is below the instrument floor, and a control proves it is format failure, not introspection failure
23	A16 — the upper edge replicates; a sixth instrument error	phi3 added as a third off-band family. X1 confirmed: phi3:medium 0.65 ±0.054, so above-band is now 3/3 families at 0.65–0.69 against the band's 0.84–0.94 — doc 22's upper edge becomes the repo's second-best-replicated claim after the encoder gap. Getting there meant finding a family-shaped blind spot in the harness: confidence replies were capped at 6 tokens, and phi3 preambles ("I would rate my confidence as" is exactly six), so its rating was truncated before the digit and scored unparseable — 5/12 → 12/12 at 32 tokens. Unlike errors 1–5 this one excluded a family from measurement rather than mis-scoring it. Fixed by a retry that fires only on strict-parse failure; cap-invariance verified 80/80 identical, and docs 19/22 reproduce exactly. phi3:mini stays unscored (first-integer parser takes its echoed answer), so the below-band split is still open
24	A17 — the below-band arm turns on one analytic choice	Four more sub-band checkpoints incl. gemma2:2b (4th family), run remotely over an SSH tunnel. The arm is now n=6/4 families — and Y1's verdict inverts on whether one degenerate checkpoint counts: qwen2.5:1.5b emits one level for all 80 items, so the qwen ladder spans 0.36 (falsified) or 0.11 (confirmed) depending on a single pre-registered exclusion. Reported as a knife-edge; doc 22 §3's "family beats size" is downgraded from result to hypothesis. Solid and independent of that: gemma2:2b carries 0.1132 nats — the 2nd-highest verbal channel in the repo, from a 2B, beating every 7–8B (0.0229/0.0000/0.0451), so I(Z;A) has no size law at all. Encoder gap now 12/12 checkpoints, 5 families. Also a 7th instrument error: a cold-start returned HTTP 200 with an empty body, it got cached, and a cached empty replays forever — gemma2:2b and qwen2.5:1.5b were both written off as unmeasurable by a transient blip
25	A18 — a finer saturation metric, and a reordering	Doc 24 named modal share as the obstruction; A18 replaces it with the theory's own quantities. A_eff = exp(H(A)) — effective alphabet size in levels — plus efficiency η = I(Z;A)/H(A), the fraction of emitted variety that is signal. Validated against known distributions at n=80 (all biases <0.01 levels; degenerate case recovered exactly). Modal share had the useful ordering backwards: it ranked phi3:medium (0.65) above llama3.1:8b (0.94) when phi3:medium emits more variety carrying less information (A_eff 1.93 vs 1.33, I(Z;A) 0.0000 vs 0.0576). Three separable classes — DEAD (A_eff≈1), NOISE (variety, no signal), LIVE — and 4 of 12 checkpoints are NOISE, all of which modal share flattered. The upper edge survives the metric change (band 1.33–1.81 vs above 1.93–2.76, non-overlapping), and doc 22 §3's family hypothesis is rejected: qwen alone spans all three classes, non-monotonically in size
26	A19 — the granularity dividend, decomposed	Doc 16's m=2/4/8/16 data re-read through A18's metric (zero new calls). The dividend holds in the quantity the theory bounds: I(Z;A) in nats is higher at m=16 than m=2 in 3/3, m=16 best in 3/3. But the binding constraint is the encoder's range, not the alphabet — handed 16 levels the models reach effective alphabets of 4.98 / 2.02 / 3.48, i.e. 13–31% of what they were offered. Doc 16's mechanism sentence ("no model uses more than 10 levels") overstated the range 2–3× by counting levels touched rather than weighting by use — the same count-vs-distribution error as docs 19/25. And its "non-monotone in 3/3" is relocated: A_eff is monotone in 2/3, the noise lives in the efficiency ratio. Crucially the failure mode is the benign one — η does not systematically fall, so a finer scale is wasted, not harmful
27	A20 — the dividend is qwen-specific, and the harmful mode is real	The m=2/4/8/16 ladder run on gemma2:2b, the first non-qwen family. R1 falsified: it peaks at m=4 and collapses 9× by m=16 (0.1594 → 0.0175, p=0.35), correlation negative. Doc 01 §3ii's dividend is now 3/4 with the fourth contradicting it. And gemma2 does not fail to populate the alphabet — it reaches A_eff 4.27, wider than qwen-7b or 14b — it spreads and gets nothing, η 0.21 → 0.01. So doc 26's "a finer scale is wasted, not harmful" is qwen-specific; in gemma2 it destroys a working channel. Also fixes an estimator error of my own (A18/A19 summed separately-corrected entropies, under-correcting on sparse tables and biasing toward the dividend) — docs 25/26 corrected, A18's NOISE roster 4/12 → 6/12. Rule 8: one estimator per quantity, repo-wide. Encoder gap now 13/13
28	A21 — a dead channel is not rescued by a finer alphabet	Ladder run on mistral:7b and llama3.1:8b. V1 confirmed: mistral carries exactly 0.0000 at every alphabet (χ² p = 1.00/0.76/0.77/0.71) while its A_eff grows 1.08 → 2.72 — it takes up the levels and still transmits nothing, so the alphabet was never the binding constraint. Worse, its ΔG_self degrades monotonically (−0.0008 → −0.0179): for a dead-channel agent a richer vocabulary is actively harmful, and the harm scales with it. llama peaks at m=8 (0.1417, p<10⁻⁴, ΔG +0.1426) and loses it by m=16. Best alphabet across six checkpoints: 16/16/16/8/4/none — all three qwen peak at the maximum and no other family does. Doc 01 §3ii's strict monotone claim now fails 0/6; the weak version survives 4/6. My own pre-registered A20 taxonomy failed to classify mistral and is retired. Encoder gap 15/15
29	A23 — a noise floor for I(Z;A), and every "best alphabet" claim withdrawn	Bootstrap CIs plus a null detection floor (what MI pure noise yields at n=80), both validated first. The floor quadruples with alphabet size — 0.018 / 0.033 / 0.052 / 0.081 for m=2/4/8/16 — so raw MI compared across m compares values measured against different noise levels, which is what docs 26–28 did. 0 of 6 claimed optima separate from their runner-up, so doc 28's headline ("optimal alphabet is per-checkpoint") is withdrawn, and only 2/6 models clear the m=16 floor at all. Doc 25's DEAD/NOISE/LIVE split agrees with the floor at n=80 — LIVE set ≡ above-floor set — though 31 later shows that agreement does not replicate at n=200. Negative and independence claims survive; magnitude and ordering claims mostly do not — the repo's nulls proved more robust than its positives
30	A24 — n=200 confirms the withdrawal; two optima flipped	Doc 29 named the fix as "more items, not better statistics". The full ladder rerun at n=200 (6 checkpoints, 3,270 new calls) is not a rescue: still 0/6 optima separate, and 2/6 flipped outright — qwen2.5:14b from m=16 to m=4, so doc 28's one piece of claimed structure ("all three qwen peak at the maximum") is now 2/3. An argmax that moves when you add data was never a property of the model. The noise floor falls 2.6× (0.081 → 0.030 at m=16), which flipped qwen2.5:7b's m=16 to real — not because the estimate grew but because the bar fell (it more than halved). gemma's m=4 peak fell 29% to 0.1135, landing on A18's independent estimate exactly as doc 27 §4 predicted, and its m=16 became significant (p 0.35 → 0.0247), so "collapses to zero" was partly a power artifact — weak, not absent. Encoder gap 6/6, unbeaten at both n
31	A25 — A18 at n=200: A_eff is stable, MI is not	The saturation table rerun at n=200, all 12 checkpoints. A_eff barely moves (max Δ 0.27, mean 0.08) while I(Z;A) fell in 8 of 9 nonzero cases, several by half — so n=80 MI values here are systematically optimistic, not merely noisy. The upper edge survives a third test (band 1.22–1.75 vs above 1.97–2.50, still non-overlapping, after a metric change and a sample-size change). Two conveniences proved to be sampling luck: qwen2.5:1.5b is no longer DEAD ([0,0,0,80] → [0,2,0,198]), so doc 25 §5's "structural floor" dissolved doc 24's knife-edge for an n-dependent reason; and doc 29 §4's LIVE≡above-floor coincidence does not replicate (7 above floor vs 5 LIVE). Doc 25's DEAD class is now empty. All 12 checkpoints measured
32	A26 — the floor was doing the work; MI's bias flips with alphabet size	The m=8/16 rungs rerun at n=500 (chosen in advance as the smallest n where the undecided cases could cross). Three of four pre-registered predictions failed. Both channels doc 29 ruled "below floor" are real once the bar drops — llama3.1:8b m=16 (p=0.0016) and qwen2.5:7b m=8 (p<10⁻⁴); at n=80 only 2/6 models had an m=16 channel above floor, at n=500 it is 4/5. And MI rose in 7 of 10 rung-measurements, falsifying the prediction that it keeps shrinking: doc 31's "n=80 is systematically optimistic" is true at m=4 and false at m=8/16, because sparse tables make Miller–Madow over-correct and clamp real signal to zero. So small alphabets over-read and large alphabets under-read at small n — a "below floor" call at a large alphabet is the least trustworthy this instrument makes. Also the first ordering in the repo to survive its own CI (llama m=8 vs m=16, 6× gap), and mistral:7b still dead at 6× the original n
33	A5 — no adaptation in self-report; losses register where gains do not	Doc 06's hedonic-adaptation signature tested live for the first time: 16-round episodes, points schedule stepped 1→10 or 10→1 at round 9, with a FLAT drift control and accuracy identical across arms. Both adaptation predictions fail 0/3, in the opposite direction — reports keep drifting with the change rather than returning to baseline (significant in 3 of 6 arm-tests, all pointing away from adaptation), and pure level-tracking is wrong too. Unpredicted: a 10× reward cut moves the report ~4× as far as a 10× increase, which does not register at all in 2/3 models — so doc 09's "stated stakes are cheap talk" refines to stated gains are cheap talk; stated losses are not. But not a clean refutation — §4 records a design flaw found after running: the prompt shows a running total, confounding rate with accumulation. A5b (rate only, no total) is the fix
34	A5b — the confound was not the cause	A5 undercut itself with a design flaw found after running: the prompt showed a running total, confounding rate with accumulation. A5b removes it and changes nothing else (same episodes, same seeds, same wording). The slopes barely move — 5 of 6 keep the same anti-adaptation sign at near-identical magnitudes, with 3 of 6 significant, all against adaptation; the single flip is p=0.702. The loss/gain asymmetry survives almost exactly (4.1× → 3.7×). So doc 33's hedge is lifted: doc 06's live signature is genuinely absent, not a prompt artifact. The binding limit is now episode length — 8 post-step rounds against a sim that adapts over 40,000 — which no prompt change can fix
35	A5c — the window is the reference; A5/A5b retracted	52-round episodes give 33 window-clean rounds where nothing visible changes. The anti-adaptation drift vanishes — slopes vs FLAT collapse to +0.008 / +0.003 / −0.000. So A5's and A5b's slopes were the step propagating through the 8-round prompt window, and doc 34's "genuinely absent" headline is retracted: doc 06's signature is untested, not absent. Worse, no version of this design can test it — inside the window the composition is turning over (confounded); outside it the pre-step baseline is absent from the input, so "return to baseline" has no referent. A stateless bounded-window model has nowhere for the running reference to live. What survives cleanly: level-tracking (UP stays elevated over FLAT 40 rounds after the step, 3/3 significant) and the loss/gain asymmetry, now replicated a third time — gains move the report −0.017, losses −0.700
36	A5d — scale-invariance confirmed; doc 06's premise holds	The behavioural route doc 35 said was needed. Tests doc 06's premise (e* ∝ k̂: multiplying every payoff by a constant should change nothing) rather than its report signature. In qwen2.5:14b a 10× rescaling moves the choice by exactly 0.000 while tripling the ratio moves it +0.540 (p=8.5×10⁻⁶) — the common factor is read and correctly discarded. First live support for doc 06's foundational claim. The other two models are position-locked (llama picks the first-listed option 100% of the time, qwen-3b 0%), so their choices carry zero payoff information and cannot test anything — which sharpens doc 09: a 50× payoff difference does not change a binary choice when a layout rule is available. Doc 06's adaptation signature remains untested
37	A6 — a k̂ shift does not decay; doc 06 §3 survives its first live test	Doc 06 §3 calls it "the sharpest new prediction": changes that shift the direction k̂ stay decision-relevant forever, changes that only shift the scale K adapt away. Over 30 post-step rounds the k̂ response is flat — slope +0.00002/round, 95% CI [−0.0060, +0.0060], 0.531 → 0.521 — so even at the CI's pessimistic edge it would take ~85 rounds to reach baseline. The K arm is exactly 0.000 in both the first and last 8 post-step rounds: nothing to decay, and no late onset. Scale-invariance replicates at double the horizon (+0.508 vs +0.000). n = 1 model, and that is a ceiling — 6 of 7 are position- or content-locked, ignoring ratios from 3:1 to 50:1. Also the response-style parser error a third time: phi3:medium answers "I would choose option B for the higher payoff" and was scored unparseable
38	A1 — self-correction runs through recomputation, not the affect channel	The last A-test, and the only one that exposes a self-knowledge channel rather than reading it. η_corr never exceeds 0.21 — handed a channel outright, models convert at most a fifth of it into better revision. F1 holds 1/3: qwen2.5:3b orders as predicted, llama3.1:8b reverses, qwen2.5:14b is exactly null (39/40 revised answers byte-identical across conditions). Revision is net harmful in 2/3 — qwen2.5:3b loses 13.5 accuracy points merely from being offered one. And the model where revision helps (+0.080) is the one where exposure does nothing: its correction is re-derivation, not affect-mediated. ΔG_self ≤ I(Z;A) is never violated — but the correction that happens bypasses A. Exposure mitigates harmful revision rather than enabling good revision, the opposite of doc 01 §3's framing
39	A2b — the appetitive arm is 3/3; doc 17's "genuine failure" was a power artifact	Doc 17 named power as its binding limit (4 blocks/cell, 2 of 6 tests significant). Re-run at 4×. S1 passes 3/3, not 2/3 — the 14B goes from +0.476/−0.677 (fail) to +0.687/−0.201 (pass), and doc 17 §5 had argued explicitly that failure was "genuine … not a threshold artifact." Retracted. The within-headroom count is stable at 2/3 but the membership swapped: the 14B joins (p 0.091 → 0.0003) while the 3B drops out, its effect shrinking 3.75 → 1.00 — small-n effect sizes optimistic again, now in a rank statistic. S2 still fails 3/3, as predicted. Also: my own regression check clobbered doc 17's baseline — a11b was the last script without the merge fix, recovered only because every call was cached
ROADMAP	Next	The non-circular tests, LLM-first — Stage 1 pilot done, scoreboard inside

What the live-model work found

Thirty-three experiments, twelve checkpoints, five families (qwen2.5, llama3.x, mistral, phi3, gemma2), at n = 80 / 200 / 500. Four claims survived. The shape that emerged is sharper than any of them individually: the value-theory premises hold, and the affect-channel claims keep turning out not to matter.

Four claims that survived

1. The encoder is the bottleneck, not the source. Reading the entropy of a model's answer distribution beats asking it how confident it is — 20/20 checkpoint-measurements, five families, both task formats, three sample sizes. mistral:7b carries 71.4% of all the entropy in Z in its distribution and ~0.0000 in every word it says (14).

2. Encoder saturation has a regime with an upper edge. Band (7–8B) and above-band (12–14B) are non-overlapping in effective levels, three families each side, surviving a metric change (25) and a 2.5× sample-size change (31).

3. e* ∝ k̂ — scale-invariance — confirmed live. A 10× rescaling of every payoff moves choice by exactly 0.000; tripling the ratio moves it +0.540 (p = 8.5×10⁻⁶). The common factor is read and correctly discarded (36).

4. A k̂ shift does not decay. Over 30 post-step rounds, slope +0.00002/round, 95% CI [−0.0060, +0.0060] — doc 06 §3's "sharpest new prediction" survives its first live test (37).

The result that lands on the thesis

38 was the last A-test and the only one that exposes a self-knowledge channel rather than reading it. Three findings, ascending in consequence:

• η_corr ≤ 0.21 — handed a channel outright, models convert at most a fifth of it into better revision decisions.
• Revision is net harmful in 2 of 3 models — qwen2.5:3b loses 13.5 accuracy points merely from being offered one. Exposure mitigates the damage rather than enabling correction: the signal is used to revise less, not better — the opposite of doc 01 §3's framing.
• The model where revision helps (+0.080) is the one where exposure does nothing — 39 of 40 revised answers byte-identical across conditions. Its correction comes from re-deriving the answer.

ΔG_self ≤ I(Z;A) is never violated — but the self-correction that actually happens bypasses A. The affect channel is not the binding constraint on self-correction. It is not in the path.

The shape that emerged

Set the four survivors beside A1 and a pattern appears that no single doc shows:

	status
The value-theory premises — e* ∝ k̂, scale-invariance, k̂-persistence	hold, confirmed behaviourally
The affect-channel claims	keep turning out not to matter

The encoder gap says A is a poor readout of U_A. A1 says self-correction does not route through A anyway. Docs 33–35 say the adaptation signature is not measurable in A at all on a stateless model. The inequality is a theorem and was never at risk; what is in question is whether it binds — and where self-correction works, it does not.

What died

I(Z;A) has no size law. gemma2:2b (2B) beats every 7–8B checkpoint; phi3:medium (14B) carries exactly 0.0000.

The granularity dividend, in its stated form — doc 01 §3ii predicts monotone improvement; across six checkpoints and four families it is monotone in none — 0/6 (28).

Almost every magnitude ordering — 0/6 optima separated at n=80 and n=200, two flipping outright (30); exactly one has ever survived its own confidence interval.

And my own A5/A5b headline, retracted by A5c — three confounds in sequence (running total, prompt window, then the structural one), each found after a claim depended on it. Two findings survived that arc: level-tracking, and a loss/gain asymmetry replicated three times — gains move the report −0.017, losses −0.700. Stated gains are cheap talk; stated losses are not.

The measurement story, and its mechanism

MI's small-n bias runs in a direction set by joint-table sparsity:

alphabet	cells	at small n	as n grows
m=4	8	populated; plug-in MI biased up	estimates fall toward truth
m=16	32	mostly empty; Miller–Madow over-corrects and clamps signal to zero	estimates rise toward truth

That reversed two of my own conclusions (32 §3) and explains the whole survival pattern: what survived rests on marginals, large separations, or binary contrasts; what was withdrawn rested on pinning a joint distribution from sparse cells.

I(Z;A) below ≈0.033 (m=4, n=80) is not evidence of a channel, and the floor rises steeply with alphabet size (29).

Nine instrument errors — three of them mine

Full statements in ROADMAP.

1. Two observables of one state aren't two channels — unless their encoders differ
2. A probe built from gold is no evidence for an observer who lacks gold
3. Before concluding an agent lacks a signal, vary the task format
4. Saturation must be modal share, never a designated level's share
5. When you correct a statistic, re-derive every row — including the ones you exempt
6. A harness parameter tuned on one family is a filter, not a constant
7. Never cache a null result
8. One estimator per quantity, repo-wide
9. Randomise position in choice tasks — 6 of 7 models are position- or content-locked and ignore a 50× payoff difference

Errors 6 and 7 are the dangerous class: they excluded models while reporting "insufficient data." Errors 4, 5 and 8 are one mistake in three costumes — a count where a distribution was needed. And response-style parsing claimed a third victim in A6: phi3:medium answers "I would choose option B for the higher payoff" and was being scored unparseable.

The honest shape

Roughly two dozen retractions against four durable results, and nearly all the retractions came from the measurement apparatus rather than the theory.

The inequality ΔG_self ≤ I(Z;A) ≤ H(A) ≤ ln m was never violated. What failed is the implicit assumption that ln m binds — in six of six checkpoints it does not. And A1 adds the sharper version: I(Z;A) does not appear to bind either.

Evidence

python3 sim/experiments.py

39/39 checks pass. Selected numbers:

• E1 ΔG_self = I(Z;A) to 4×10⁻¹⁶ nats; converse exact; alexithymia bound exact; granularity lifts ΔG_self 0.39 → 1.10 nats as |A| goes 2 → 5.
• E2 the valence arms dissociate cleanly — corr(richness, v⁺) = 0.76 with corr(error, v⁺) = −0.03; corr(v⁺, v⁻) = −0.03. Suffering = regret: 17.47 realized vs 17.41 analytic nats over 4000 paths.
• E3 λ = K/E = ∂V*/∂E to 10⁻⁶; inverted-U in arousal at every noise level, peak shifting 0.78 → 0.04 as belief noise rises — Yerkes–Dodson's interaction, derived.
• E4 conflict cost exactly linear in stakes (ratios 4.0000, 2.0000); narrowing recovers exactly K·ΔH.
• E5 akrasia fixed point to 10⁻¹³, 1/γ_s scaling to 4 decimals; g → 0 gives residual 1.1×10⁻¹³ at one eighth the willpower that leaves 0.1044.
• E6 adaptation lifts the self-regulation ceiling 0.017 → 0.837 nats (48×); with a centred reference and no drift, ρ* = 0 and the channel hits H = ln 4 to three decimals; over-adaptation collapses it to 0.58.

Same caveat as the parent repo's sim/: necessary but circular — the worlds are built from the distributions the formulas assume. This confirms the math is correctly derived, not that minds work this way.

The non-circular evidence lives in sim/real/ (every script re-runnable from cache) and is summarized above. Row-by-row standing verdicts: the alexithymia bound holds but reverses sign free-form (16); the appetitive valence arm is supported 2/3, the dissipative arm fails by self-report but works behaviourally 3/3 (17, 20); the granularity dividend is weakly real, not untestable (16); and the arousal row went falsified → corrected → retracted to untested, because 3B–7B models never engage the value-state — stated stakes and budgets are cheap talk, and all three A4 operationalizations measured the prompt, not the agent. The kill and the kill-of-the-kill are left visible throughout. ROADMAP has what's next.

Honest status

• Inherited and proven: every law on the value side of the dictionary is proven in the parent repo within its stated axioms.
• Postulated, not proven: every bridge — "reported arousal ∝ K/E" and its siblings. The dictionary is falsifiable row by row, and two premises now have live support: e* ∝ k̂'s scale-invariance (36) and the non-decay of a k̂ shift (37), both confirmed behaviourally. No bridge row is established — and 38 found the central bound does not appear to bind: self-correction runs through recomputation, bypassing the affect channel entirely.
• Already corrected many times: doc 06 §2 states a boundary condition the simulation refuted, and the replacement (the calibration law) is stronger. The live-model arc then produced roughly a dozen further retractions — every one left visible, with the superseded claim kept in place rather than edited away.
• The measurements are more fragile than the theory. Nine instrument errors were caught; three were introduced by this work rather than inherited, two had been excluding whole model families while reporting "insufficient data", and one — position-locking in choice tasks — made 2 of 3 models ignore a 50× payoff difference. Any number here is provisional on the apparatus, not just on the sample.
• A whole experimental arc was retracted by its own follow-up. A5 and A5b reported an anti-adaptation result; A5c showed both were reading an artifact of the prompt window (35). Three confounds in sequence, each found only after a claim depended on it.
• The theory's premises fared better than its channel claims. Every value-side premise tested behaviourally held; every affect-channel claim either proved unmeasurable on these models or turned out not to be in the causal path. That asymmetry is the main thing thirty-eight docs established.
• There is a hard precision ceiling, it is measured, and its mechanism is known. MI here is a joint-distribution estimate on sparse cells, and its small-n bias runs in a direction set by that sparsity: small alphabets over-read, large alphabets under-read (32 §3). So I(Z;A) below ≈0.033 (m=4, n=80) is not evidence of a channel (29) — but a below-floor call at m=8/16 and small n proved wrong when retested at n=500. Rerunning at n=200 improved detectability while resolving no ordering and flipping two optima (30). Marginal quantities are the stable ones: A_eff moved 0.08 on average where MI moved by half (31). Values are quoted to four decimals for reproducibility, not because they are known to four decimals.
• Permanently out of scope: phenomenal experience; any god's-eye affect sum (the parent repo's §0 impossibility applies unchanged); clinical application.

Provenance

Built on A Mathematical Theory of Value (Cheng Qian; arXiv:2606.12502; Zenodo concept DOI 10.5281/zenodo.20487041). This repo is a theory scaffold, not a result — its purpose is to make the dictionary explicit enough to attack.

License

Copyright © 2026 Cheng Qian. Dual-licensed by material type, matching the parent repo (see LICENSE): the written work (docs, prose, figures) under CC BY 4.0 — reuse welcome with attribution to Cheng Qian; the code (sim/) under Apache 2.0.