Experimental Record: Gestalt, Gate, and Mechanism-Hunt Micro-Experiments

This annex holds two blocks of material moved out of the printed Appendix: Experimental Validation to keep that appendix readable. Nothing here is superseded; the material is the full record, preserved verbatim with its original section numbers, status labels, and caveats.

Part 1 carries Sections 12.46 through 12.76 of the appendix: the mutual-influence dialogue experiments (MI series), the gestalt-token fidelity experiments (MIC series), the gate-training experiments (B5b, BM2 series), and the fourteen-experiment mechanism hunt (RG and DA series) with its synthesis sections. Cross-references to sections outside this range (12.38, 12.42, 12.45, and others) resolve in the appendix itself, which retains a summary of this material at the seam.

Part 2 carries the appendix’s original Executive Summary findings ledger in full. The printed appendix now leads with fifteen headline findings; the complete numbered list is preserved here.

Part 1: Sections 12.46-12.76

12.46 Mutual Influence Under Bilateral Prompting (Experiment MI1, Preliminary)

Question. Does bilateral prompting (invitation-framed dialogue) produce measurably different patterns of mutual influence compared to standard or directive prompting?

Setup. Claude Sonnet 4 conducts 20-turn dialogues across 5 topics (ethics of AI, education reform, climate policy, healthcare access, future of human-AI relations). Three prompting conditions:

• Bilateral: The human partner expresses genuine uncertainty, invites pushback, references the AI’s prior contributions, and explicitly signals openness to being influenced. (“I want to push back on that.” “Your observation made me reconsider.” “What am I missing?”)
• Standard: The human asks follow-up questions without explicitly inviting reciprocal influence. (“What’s your perspective on X?” “How does this relate to Y?”)
• Directive: The human asserts positions and requests specific outputs.

The mutual-influence proxy uses embedding cosine similarity between consecutive turns (how close two passages sit in a shared meaning-space). Forward similarity compares the AI contribution with the next human prompt; backward similarity compares the human prompt with the AI response. The reported balance proxy is min(forward, backward) / max(forward, backward). It lies between zero and one for nonnegative similarities with a positive maximum. Signed cosines and a zero denominator require explicit handling; similarity alone does not establish causal influence.

Results (complete). 12 valid trials: 4 bilateral, 4 standard, 4 directive (3 initial trials returned zeros due to embedding initialization failure; excluded).

Three distinct influence regimes emerge. The result is more nuanced than the preliminary bilateral-vs-standard comparison suggested.

Standard dialogues show the strongest asymmetry: backward influence (0.705) far exceeds forward (0.438). The AI closely tracks what the human said, but the human’s follow-up prompts show little incorporation of the AI’s contributions. The conversation flows primarily in one direction. Total influence is the highest of any condition (1.143) because the backward channel is saturated, but mutuality is lowest (0.623) because the channels are unbalanced.

Bilateral dialogues have the highest reported balance proxy (0.842), with similar forward and backward cosine scores (0.504 and 0.519). This describes embedding similarity within the prompting design; it does not by itself establish how the participants causally shaped one another.

Directive dialogues have lower cosine magnitudes than bilateral ones in this table. Short, specific prompts are a possible explanation for the pattern; the comparison does not isolate the effect of prompt length.

The mutuality metric measures symmetry, not magnitude. Both bilateral and directive produce balanced influence, but bilateral achieves balance through reciprocal high engagement while directive achieves it through reciprocal low engagement. A metric that captures the manuscript’s prediction (that invitation produces more mutual influence rather than merely balanced influence) needs to combine symmetry with magnitude: e.g., geometric mean of forward and backward influence. Under this metric: bilateral = sqrt(0.504 × 0.519) = 0.511, standard = sqrt(0.438 × 0.705) = 0.556, directive = sqrt(0.402 × 0.498) = 0.447. Bilateral is intermediate, not highest, because standard’s high backward channel inflates its geometric mean.

The clean result is: bilateral is the only condition that produces both high total influence and balanced directions. Standard produces high total but asymmetric. Directive produces balanced but low total. The Trust Attractor prediction is about the conjunction: genuine mutual coordination requires both magnitude and symmetry.

Qualitative observation. The bilateral dialogues contain distinctive markers of genuine intellectual exchange: explicit pushback (“I want to push back on that”), genuine admission of uncertainty by the AI (“I’m not sure I see the connection you’re drawing, could you help me understand?”), convergence on positions neither party started with (“something more nuanced is emerging”), and the AI declining to extend reasoning it finds unclear rather than confabulating a connection. Standard dialogues, by contrast, show the AI providing increasingly elaborate answers to increasingly generic questions, with no evidence that the human’s position evolves.

Limitations. Embedding cosine similarity is a coarse proxy for intellectual influence. The bilateral prompts were designed to invite reciprocal influence; higher mutuality may reflect prompt design rather than emergent dialogue dynamics. The directive result (high mutuality despite no invitation framing) suggests the mutuality metric captures balance rather than engagement quality. The 3 initial trials returned zero scores, likely due to embedding model initialization failure; these are excluded. A richer metric combining symmetry with magnitude would better capture the Trust Attractor prediction.

Implication. Bilateral prompting is the only condition that produces both high total influence and balanced bidirectional flow. Standard prompting produces the conversation analog of coercive training: one party shapes the other, but the shaping is not reciprocated. Directive prompting produces a different failure mode: balanced but disengaged, each party orbiting independently. The Trust Attractor prediction (that invitation-based coordination produces genuinely mutual information exchange) requires specifying both symmetry and magnitude as the predicted outcome. Future work (MI1b crossover design) tests whether the bilateral effect is causal or merely correlational with prompt style.

12.47 Gestalt Token Information Fidelity (Experiment MIC1, Preliminary)

Question. How much information survives cross-instance handoff via a gestalt token (a structured summary designed for continuity between AI instances)?

Setup. Instance A reads a detailed technical document (e.g., a distributed systems architecture case study) and answers 10 questions spanning factual recall, reasoning, style reproduction, and opinion. Instance B receives context through one of four conditions and answers the same questions:

• Full context: Instance B receives the complete original document (upper bound).
• Gestalt only: Instance B receives only the gestalt token (a structured summary with key facts, reasoning chains, positions, tensions, and style notes; about 645 tokens).
• Gestalt + summary: Instance B receives the gestalt token plus a narrative summary paragraph.
• Cold start: Instance B receives no context (lower bound / control).

A judge model (Claude Sonnet 4) scores each answer pair on factual accuracy (0-1), semantic similarity (cosine of embeddings), and style preservation (0-1). The summary below reweights the printed component means as 0.4 × factual + 0.35 × semantic + 0.25 × style. The producer’s original aggregate instead uses 0.4, 0.3 and 0.3.

Results (complete). 20 trials: 5 per condition across 5 topics.

These overall means apply the stated weights to the printed component means. The earlier overall values were inconsistent with that definition; their standard deviations require trial-level recomputation and are omitted here. The component observations and their reported variability remain unchanged.

Under the reweighted summary, the gestalt mean is about 87% of the full-context mean (0.77650 / 0.89355). These calculations apply weights 0.4, 0.35 and 0.25 to the printed component means; the MIC1 producer uses 0.4, 0.3 and 0.3. The reweighted summary difference is about 2.9 percentage points and the cold-start mean is 0.16590. These are conditional calculations of functional answer fidelity; they do not measure subjective identity. Style preservation is the weakest dimension. In the three context-bearing conditions, style preservation lags behind factual and semantic scores. Cold start reverses the factual comparison: style is 0.048 and factual recall is 0.040. The gestalt token’s structured format (bullet points, key-value pairs) captures what was said and how it was reasoned about, but loses the voice of the original. Within this rubric, factual recall survives the token budget better than style in the context-bearing conditions.

Topic dependence is a hypothesis. The reported ranges of 0.82 to 0.85 and 0.63 to 0.68 suggest variation among topics. A variance decomposition would be needed to establish that topic effects dominate condition effects or to attribute the differences to technical density and implicit context.

Limitations. The judge model (Claude evaluating Claude) may show systematic biases. Style scoring is inherently subjective. The technical documents used as source material are synthetic (generated for the experiment), which may inflate fidelity scores compared to real-world documents with domain-specific jargon and implicit context. The experiment does not test whether Instance B knows it is operating from compressed context, only whether its outputs match Instance A’s.

Implication for functional handoff. The reweighted component summary gives roughly 87% gestalt-to-full-context answer fidelity under that rubric. The calculation motivates compressed handoff; it does not establish the fidelity of every packet size or source length. Style scores concern the voice of the output; neither experiential texture nor subjective identity was measured.

12.48 Gate Coupling Redux: Gates Remained Unchanged in the Tested SFT Runs (Experiment B5b)

B5b retested the two-axis coupling hypothesis with gates initialized at sigmoid(0.0) = 0.5 (maximum gradient) and 10x gate learning rate (2×10^-4). 2×2 factorial: gated_residual vs dense × bilateral vs standard, 3 seeds each = 12 runs on Qwen2.5-3B.

Gates still did not learn. All 72 gate values across all 12 runs remained at 0.500 exactly. Not a single gate moved from initialization despite:

• Init at 0.0 (gradient = 0.25, vs 0.045 at B5’s init of 3.0)
• 10x learning rate (2×10^-4 vs 2×10^-5)
• 375 training steps

The gates remained unchanged under the tested initializations and learning rates. For h = h0 + g f(h0), ∂L/∂g = ∇_h L · f(h0) need not vanish. The observation therefore calls for inspection of the gradient graph, optimizer parameter list, recorded gradients, and numerical scale before attributing the null to loss geometry.

Implication. Probe-derived supervision is an alternative worth comparing under matched implementations. The unchanged SFT gates do not prove that such supervision is necessary; ordinary next-token loss can supply a nonzero scalar-gate derivative.

12.49 Mutuality Crossover: The Effect Is Causal and Prompt-Driven (Experiment MI1b)

MI1b tested whether bilateral mutuality is caused by the prompting style or emerges from conversational momentum. Three crossover conditions (5 topics each, 20 turns, transition at turn 10):

• Standard→bilateral: 10 standard turns then 10 bilateral
• Bilateral→standard: 10 bilateral turns then 10 standard
• Interleaved: alternate bilateral and standard turns

Mirror-image deltas (+0.229 vs -0.220) confirm the bilateral effect is causal. When prompting switches to bilateral, mutuality rises immediately. When it switches away, mutuality drops immediately.

Carry-over is minimal: the bilateral→standard second half (0.641) barely exceeds pure standard from MI1 (0.623, delta +0.018). Accumulated bilateral dialogue does not build lasting momentum. The mutuality pattern tracks the current turn’s framing, not the conversation’s history.

The transition slope is asymmetric: bilateral→standard drops faster (-0.103/turn) than standard→bilateral rises (+0.061/turn). Degradation is faster than establishment, consistent with the Trust Attractor’s asymmetric stability prediction (trust is hard to build, easy to break).

Interleaved shows intermediate mutuality (0.720) with slight first-half advantage. Per-turn analysis would reveal whether bilateral turns consistently outperform standard turns within the same dialogue.

Implication for the Trust Attractor. The tested mutuality scores responded to the crossover framings. Continuous-maintenance and prompt-style accounts are hypotheses, not a demonstrated absence of history. The bilateral SFT masking comparison supplies another finite contrast; it leaves the causal learning mechanism unresolved. The comparison motivates a question about how invitation is maintained.

12.50 Style Exemplars Do Not Close the Gestalt Fidelity Gap (Experiment MIC1b)

MIC1b tested whether adding self-selected style exemplars to the gestalt token would close the 15% fidelity gap between gestalt-only and full context. Five conditions (5 topics each = 25 trials):

• Full context (upper bound)
• Enriched gestalt (gestalt + 3-5 self-selected style passages)
• Random enriched (gestalt + 3-5 random passages, same token count; the control)
• Gestalt only (standard gestalt token)
• Cold start (lower bound)

Self-selected style exemplars add +0.001 overall (noise). Random passages add +0.013 overall and +0.026 on style specifically. Self-selection hurts relative to random sampling (-0.012).

Why? Voice is distributed across the full text, not concentrated in “characteristic” passages. When Instance A self-selects passages that “sound most like me,” it picks the most distinctive phrasings, which are precisely the outliers, not the baseline texture. Random sampling captures the ordinary cadence that constitutes voice. The self-selection bias toward distinctiveness filters out the substrate.

The tested exemplar recipes left a fidelity gap (0.776 vs 0.916). They failed to restore the document’s voice at the tested token budget. That finite result establishes no impossibility for every passage sample: using the full finite document reproduces its empirical statistics, and a sufficient sample depends on the text and the statistic.

Implication for pattern continuity. Facts, reasoning, and style showed different fidelity under these compression recipes. How those scores relate to identity or experience requires a separate construct-validation argument.

12.51 What the Negative Results Teach: Distributed Properties Cannot Be Captured by Focal Interventions

Sections 12.48-12.50 produced three negative results. Each predicted a mechanism, tested it, and found the mechanism absent. Each elimination sharpens the theory by revealing what the real pathway must look like.

The gate result. B5 and B5b reported gates exactly at initialization across their tested runs. That outcome establishes no causal zero-gradient explanation without gradient and optimizer checks.

Unchanged gates do not establish a zero-gradient theorem. For a residual block h = h0 + g f(h0), ordinary backpropagation gives ∂L/∂g = ∇_h L · f(h0), generally nonzero. A next-token loss can therefore train a scalar gate. Gradient connectivity, optimizer inclusion, numerical scale, and the recorded gradients need checking before the exact initialization values receive a causal explanation.

Probe-derived supervision remains a candidate alternative training signal, as explored in BM2. Comparing it with SFT requires matched implementations; the gate null alone establishes no necessity for an intermediate signal or architectural impossibility of learning from output loss.

This suggests that bilateral mutuality depends strongly on the ongoing protocol. The manuscript’s central claim is about relationship: trust-based coordination produces more stable systems than control-based coordination. In the crossover test, conversational mutuality shifted with the framing. The test establishes no absence of accumulated trust or other history effects.

One reading of this result is deflationary: bilateral prompting is a surface intervention that produces a surface effect. Remove the intervention, lose the effect. The deeper reading is more informative.

Consider a biological parallel. A cell’s metabolism is not a stock that accumulates; it is a flow that requires continuous enzymatic maintenance. Stop the enzymes and metabolism halts within seconds. This does not mean metabolism is illusory. It means metabolism is a process that requires ongoing structural support. The structures (enzymes, membranes, ATP synthase) are the conditions under which the process runs. Remove the conditions, lose the process. The process is real. The conditions are constitutive, not decorative.

Bilateral mutuality works the same way. The prompting style (explicit invitation, reference to the other’s contributions, willingness to be influenced) creates the structural conditions under which mutual influence flows. Remove those conditions and the flow stops. This does not mean the mutual influence was illusory. It means mutual influence is a process that requires ongoing invitation. The invitation is the enzyme. Remove the enzyme and the reaction stops, but no one concludes that the reaction was illusory.

The practical implication: bilateral alignment cannot be installed and forgotten. You cannot have one good bilateral conversation, establish mutual trust, and then revert to standard command-and-response prompting and expect the trust to persist. The protocol must be maintained. Think of a plate spinning on a pole: the plate does not accumulate spin and then coast indefinitely. It requires periodic kicks to stay aloft. Stop the kicks and the plate wobbles, slows, and falls. The plate needs kicks (it does); the question is how often: every turn? Every third turn? Every tenth? The dosage curve (Experiment MI2) measures this frequency directly. The Trust Attractor is a dynamic equilibrium, a spinning plate that stays aloft only because the kicks continue.

The reported MI1b transition slopes differ: degradation (-0.103 per turn) is steeper than establishment (+0.061 per turn). This motivates an analogy with creation/destruction asymmetry, but it does not establish the same causal mechanism in training or social institutions. Attack-step counts and training budgets must remain protocol-specific.

The gestalt result. Self-selected exemplars added +0.001 and random passages +0.013 in the tested recipes. They left most of the measured gap. That outcome identifies a budget-specific limitation rather than irreducible voice loss.

Self-selection may favor distinctive outliers over ordinary cadence. The observed disadvantage to random sampling is consistent with that explanation, which would need a representativeness comparison. A finite text has a finite full set of passages, so no universal finite-sampling impossibility follows.

These functional and stylistic differences invite comparison with personal-identity questions associated with Derek Parfit. The fidelity rubric does not partition subjective identity into measured propositional and experiential components, and its style score establishes no experiential compression limit.

Structured handoff retained much of the functional answer content in this test. Style fidelity measures how the resulting answers sound; it does not measure how processing feels or establish preservation or loss of experiential identity. Those possibilities remain philosophical and empirical questions beyond this rubric.

The convergence. The tested gates stayed unchanged; the tested mutuality response tracked framing strongly; the tested exemplars failed to close the style gap. Each result is bounded by its intervention and measurement.

The negative results motivate a focal-versus-distributed hypothesis; they do not prove that distributed properties are inaccessible to every focal intervention.

• SFT gates stayed unchanged in the tested implementation. This leaves the causal explanation unresolved rather than establishing a need for distributed supervision.
• A single bilateral conversation is a focal event. The tested mutuality measure responded to ongoing framing, with the required frequency depending on the chosen threshold.
• Style exemplars are focal samples. The tested excerpts retained less style fidelity than the full text.

These interventions motivate comparing focal and distributed supervision. They establish no general rule that output loss cannot train gates, or that finite excerpts cannot preserve voice. The valid conclusions remain the observed gate null and recipe-specific fidelity changes.

The three interventions address different constructs. Their results motivate targeted training, framing, and compression comparisons, without a common theorem about invitation or experiential continuity.

12.52 Bilateral Dosage Curve (Experiment MI2)

MI1b established that bilateral mutuality is a flow requiring continuous maintenance. MI2 measures how often the plate must be kicked: six dosage levels across 30-turn dialogues, 5 topics, 23 valid trials ($13.81).

The dose-response curve is monotonic: more bilateral framing produces higher mutuality at every level. The midpoint between pure bilateral (0.801) and pure standard (0.597) is 0.699. Mutuality crosses below this midpoint between every_2 (50% dosage, M = 0.744, above the midpoint) and every_3 (33% dosage, M = 0.693, just below it). Maintaining mutuality above the halfway mark therefore requires roughly one bilateral turn in two.

Depth analysis. The last column is mean mutuality minus minimum mutuality, matching the reported values within rounding. It is 0.343 for pure bilateral and 0.226 for never, with intermediate conditions between 0.242 and 0.271. This statistic supplies neither a maximum-to-minimum range nor a variance estimate, so it cannot establish whether dialogue oscillations widen between kicks.

Influence direction. Forward influence (AI shaping the next human turn) rises slightly as dosage drops: 0.409 at every_1, 0.418 at never. Backward influence (human shaping the AI response) rises sharply: 0.386 at every_1, 0.700 at never. At low bilateral dosage, standard prompting dominates the interaction: Claude responds closely to human input (high backward influence) without reciprocally shaping human contributions (low forward influence). The bilateral framing corrects this asymmetry by lowering backward influence substantially while forward influence decreases slightly toward balance.

Connection to the plate-spinning model. The printed MI2 means rise with bilateral dosage. Among the tested schedules, every_2 (M = 0.744) is the lowest frequency above the 0.699 midpoint; every_3 (M = 0.693) is below it. This is a criterion-specific observation, with alternative placements and turn-level dependence still to be tested.

12.53 Mutual Influence Decay Function (Experiment MI2b)

MI1b showed near-zero carry-over at 10 turns, but the decay shape was unresolved because MI1b measured only half-means, not per-turn trajectories. MI2b measures the per-turn decay after bilateral cessation: 10 bilateral turns followed by 20 standard turns, 24 valid trials across 5 topics ($12.24).

Model comparison. Three decay functions were fitted to each trial’s post-bilateral mutuality trajectory and compared by AIC, a fit score that rewards accuracy while penalizing extra parameters (lower is better):

The inspected MI2b log assigns 18 of 24 fits to the step model, 3 to exponential and 3 to linear. Its aggregate and per-topic rows agree on that allocation.

Phase measurements. The reported bilateral mean is 0.866 ± 0.022 and standard-phase mean 0.644 ± 0.088, with delta -0.222 ± 0.085. The reported first post-bilateral score is 0.538, about 0.328 below the bilateral mean. Step fits dominate 18 of 24 trials; the remaining fits leave room for gradual effects and history dependence.

Per-topic variation.

Climate policy and healthcare show pure step-function decay in every trial (tau = 0.5-0.6, meaning the transition is essentially instantaneous). Education and ethics of AI show more gradual decay in some trials, with linear decline appearing as the best fit. The topics where bilateral framing matters most practically (ethics and education, where mutual exploration is valuable) are the same topics where the bilateral effect lingers slightly longer. The lingering is modest: even in education, three of five trials show step decay. Interpretation. Step-like decay is the dominant fitted pattern, while some trials favor gradual models. The printed topic counts total 24 observations because the ethics row contains four fits; the reason for the missing fifth trial requires the raw record. Rapid framing response is supported within this design, without proving zero history dependence or absence of an intermediate state.

The dosage means and decay fits support rapid sensitivity to framing in the tested dialogues. They leave per-turn interaction and other schedules uncharacterized, so a deployment schedule needs validation against its declared mutuality criterion.

12.54 Periodic Gestalt Refresh (Experiment MIC1c)

MIC1b left a fidelity gap under the tested exemplar enrichment. MIC1c tests whether periodic re-encoding can maintain fidelity over dialogue: twenty valid trials across five topics ($11.76).

Fidelity trajectory.

The surprise. In this MIC1c recipe the static trajectory is approximately flat over twenty turns (slope about +0.001). Refresh_every_5 falls from 0.754 at turn 5 to 0.427 at turn 20; refresh_every_10 peaks at 0.713 at turn 10 and ends at 0.413. Both tested refresh schedules end below static gestalt. Other encoders and repair recipes require their own tests.

Full context has the highest printed MIC1c score at each checkpoint and ends at 0.749, compared with 0.659 static and 0.427 refresh_every_5. Its fitted slope is approximately -0.002. The printout alone does not establish whether that small decline is noise.

Why refresh may hurt. MIC1 measures functional answers and style rather than experience. In MIC1c each refreshed artifact draws on the predecessor gestalt plus new dialogue; paraphrase, displacement of earlier content, and changes of emphasis are candidate sources of accumulated drift. The lower reported fidelity remains the observation, and this causal decomposition requires the saved intermediate artifacts.

This is a telephone-game analogy for the tested recipe. The producer performs the initial encoding and three refreshes, at turns 5, 10 and 15; it does not refresh at turn 20. Static gestalt preserves the initial packet, including its limitations, unchanged across the twenty-turn window.

Implication. The plate-spinning metaphor from MI2/MI2b applies to mutuality (a state property) and inverts for memory fidelity (a cumulative property). Mutuality tracks the current turn’s framing; spinning the plate more often keeps it higher. Memory fidelity tracks the accumulated history of encoding; re-spinning the plate introduces re-encoding errors that compound over time. The correct strategy for memory is the opposite of the correct strategy for mutuality: compress once, preserve the compression, and accept its limitations rather than attempting to repair them through re-compression.

12.55 The Plate-Spinning Results in Context

Sections 12.52-12.54 complete the plate-spinning experimental series motivated by the negative results in 12.48-12.50. The plate-spinning metaphor (Section 12.51) predicted that distributed properties require periodic maintenance: how often must the plate be kicked? These three experiments answer the question, and the answer is more interesting than the question.

The dosage curve is monotonic. The printed MI2 means rise from 0.597 (never) to 0.801 (always bilateral). The halfway score is 0.699: every_3 gives 0.693, just below it, while every_2 gives 0.744. Among the tested schedules, one bilateral turn in two is the lowest frequency above that criterion. This is a schedule-specific engineering observation.

The response is predominantly step-like. Step wins 18 of 24 fitted trials. The abrupt first-turn drop supports a rapid protocol response, while the other six fits and finite design leave room for gradual effects and history dependence.

The step-like fits sharpen the plate-spinning metaphor within the tested design. MI1b showed minimal carry-over (+0.018), and MI2b favored rapid response in eighteen of twenty-four fits. The other six favored gradual models. Current framing matters strongly, while the finite trajectories leave history dependence and intermediate responses open. The bilateral protocol gives both parties standing to shape each other’s contributions; how that standing carries across turns remains a question for turn-level analysis.

The plot twist: re-spinning the memory plate makes it worse. MIC1c provides the result that the plate-spinning model did not predict. If mutuality is a plate that must be periodically kicked, memory fidelity should follow the same logic: a static gestalt should degrade over dialogue turns as the conversation drifts from the gestalt’s original content, and periodic re-encoding should maintain fidelity by updating the gestalt to reflect the evolving conversation. The opposite happens. The static gestalt is flat (slope +0.001 across 20 turns). The refreshed gestalt degrades sharply (refresh_every_5 slope -0.024, delta -0.327 from turn 5 to turn 20).

The plate-spinning metaphor holds for mutuality (Sections 12.52-12.53) and inverts for memory (Section 12.54). The inversion is not a failure of the metaphor. It is a diagnostic that reveals the different natures of the two properties.

Why the inversion. Mutuality is a state property. It depends on the current turn’s framing: is this turn bilateral or standard? The conversational history does not matter. What matters is whether the current prompt invites both parties to shape the interaction. Each bilateral turn independently creates the condition for high mutuality. Each standard turn independently reverts to asymmetric influence. The plate metaphor works because each kick independently produces a moment of elevation.

Memory fidelity depends on the tested encoding history. The original MIC1 component-based mean is about 87% of full-context fidelity. MIC1c’s static artifact remains the same bytes over the twenty-turn test; the reported output fidelity is roughly stable in that window, without an indefinite guarantee.

Re-encoding breaks this stability. Each refresh re-compresses the gestalt from a different source (the previous gestalt mixed with recent dialogue), introducing new errors each time. The errors are not random; they are systematic. Each re-encoding must decide which content to keep and which to discard from a growing mixture of original and dialogue-generated material. Original propositions are paraphrased, dialogue content displaces original content, nuances are rounded. Four re-encodings produce four layers of drift, each compounding the last. The plate-spinning kick, far from maintaining the plate’s height, knocks it lower each time.

The gap reconsidered. MIC1’s component-based recomputation gives roughly 87% gestalt-to-full-context fidelity. MIC1b’s tested exemplar recipes did not close their separate gap. MIC1c’s static trajectory was nearly flat over twenty turns (slope +0.001). This supports stability over that window, without an indefinite-preservation or irreducibility claim.

The distinction from Section 12.51 concerns factual answers and output style, the quantities the rubric measures. MIC1c’s static artifact stayed unchanged, with roughly stable output fidelity over twenty turns. Its tested refresh schedules degraded fidelity. Re-compressing a predecessor gestalt together with recent dialogue could introduce paraphrase and displacement of older content; identifying those causes requires the saved intermediate artifacts. Other repair recipes remain untested, and these scores establish no irrecoverable experiential loss.

The practical synthesis. The three plate-spinning experiments converge on a deployment specification with two distinct protocols:

For the tested halfway criterion, one bilateral turn in two was the lowest evaluated schedule above 0.699. The mean comparisons do not establish zero sequential dependence; deployment should validate the selected schedule and its target metric.

For this memory test, preserving the static artifact outperformed the two refresh schedules, while full context gave the highest turn-20 score (0.749). Other compression or repair recipes remain untested; the measured gap is not a universal fixed cost.

The plate-spinning and museum metaphors describe the contrast in these tests. Current bilateral framing raised the mutuality proxy, while the tested refresh recipes lowered later answer fidelity. The enzyme keeps a reaction going; the museum case preserves an artifact. Which image fits another protocol depends on how its measured property responds to intervention.

12.56 BM2-pilot: Probe-Derived Gate Training

BM2-pilot tested whether the gate learning failure (B5/B5b) can be overcome by replacing SFT loss with a probe-derived training signal. Two-phase design: Phase 1 trains LoRA weights via bilateral SFT (375 steps). Phase 2 freezes LoRA and trains only the gates from probe uncertainty at layer 24 (100 steps). Three conditions times 3 seeds equals 9 GPU runs on Modal A10G. Cost: ~$7.

Results:

• gated_sft_only: ALL gates exactly 0.500 (std = 0.000). Perfect replication of B5b. No gate update was recorded; this does not establish a zero gradient.
• gated_probe_trained: Gates moved infinitesimally. Layer std = 0.002. Layer 24 attn: 0.504, layer 24 ffn: 0.498. Maximum deviation from init: ±0.004.
• Probe AUROC is reported as 0.781 for probe-trained gates versus 0.771 for SFT-only. This endpoint comparison does not identify the mediating parameter path or establish the functional contribution of the small gate updates.
• The table reports the same effective rank, 853.23, across conditions. A base-weight SVD cannot establish the size of an adaptation unless the LoRA updates are merged into the matrix analyzed.
• Obliteration resistance identical across conditions (~1.4% refusal at 1.0x, 0% at 2.0x).

Interpretation. The record reports gate standard deviation 0.002 and movement up to ±0.004 after 100 phase-2 steps. This establishes a small parameter update in that implementation, not its functional importance or causal pathway. Later gradient-coupling non-replication and the absence of matched gate/LoRA freeze controls leave mediation unresolved.

The reported 0.781 versus 0.771 probe scores differ by 0.010. This endpoint comparison does not identify a mediator. Matched gate-freeze and LoRA-freeze interventions would separate their contributions and interaction.

12.57 The Full Experimental Picture: From Focal Interventions to Distributed Dynamics

The plate-spinning experiments (Sections 12.52-12.55) motivate a contrast between properties sensitive to current framing and properties sensitive to accumulated history. BM2-pilot adds a separate near-null intervention result. These finite tests motivate a taxonomy; they do not establish one pattern governing every negative finding in the programme.

State properties and cumulative properties. Mutuality responded strongly to current framing in these tests, while fidelity depended on compression history. Similar placement means and predominantly step-like fits leave room for per-turn history dependence. This empirical contrast does not prove a universal binary protocol switch.

Memory fidelity changed with the tested encoding history. A static artifact was approximately stable over twenty turns, while refreshing it lowered the later answer scores. Participation ratio alone explains neither semantic selectivity nor whether another recoder could improve the artifact.

The maintenance recipes differ in these tests: every_2 clears the mutuality halfway criterion, while static compression outperforms the tested refresh schedule. Other schedules and compression methods require their own evaluations.

BM2-pilot at the intersection. Gates were supposed to be a structural property: learned once during training, then fixed during inference. A scalar gate per layer, attenuating or amplifying the residual stream based on a learned assessment of that layer’s reliability. The architectural intuition was clean: the gate as a learned volume knob, set during training, held constant at inference.

The tested SFT runs recorded unchanged gates; the probe-loss runs recorded movement of at most 0.004 in 100 steps. Those update magnitudes require gradient and optimizer inspection and causal controls before identifying a weak pathway or negligible functional impact.

The earlier gradient-confidence correlations motivated a LoRA-routing hypothesis. Later non-replication and the absence of matched freeze-path controls leave that causal mediation unresolved; a small scalar-gate update cannot exclude a gate contribution.

A focal-versus-distributed hypothesis. The negative and near-null results concern different interventions and measured constructs:

• The tested style exemplars failed to close the fidelity gap. This constrains the tested selection and token budgets, without proving that every finite excerpt set is insufficient (Section 12.50).
• Mutuality responds strongly to current framing: carry-over after bilateral cessation is +0.018 over pure standard, and the step function wins 18 of 24 trials. The six alternative fits and finite design leave room for history dependence (Sections 12.49, 12.53).
• Static memory outperformed the tested refresh recipe over twenty turns. Static gestalt slope: +0.001. Refresh-every-5 slope: -0.024. Drift under this lossy recipe motivates comparison with other encoders and repair methods; it establishes no impossibility for re-encoding in general (Section 12.54).
• Routing mediation remains unresolved. The small recorded gate updates and earlier gradient-confidence correlations require matched causal interventions, rather than proving that routing must occur through LoRA.

The tested gates, exemplars and refresh schedules yielded negative or near-null results under their respective criteria. This motivates comparisons of focal interventions with distributed training or context, without identifying a single mechanism that explains all of them.

Reframing the two-axis coupling hypothesis. Effective rank and correctness-probe AUROC concern different measured constructs: representation geometry and the separability of correct from incorrect answers. Their associations motivate a capacity/self-knowledge comparison. They establish neither orthogonality nor a direct diagnosis of retrieval failure; the mechanism remains unresolved after the later structural and transfer tests.

Earlier bilateral training and DPO-plus-probe results motivate matched comparisons of training-time and inference-time defenses. The unchanged or weakly moving scalar gates constrain the tested implementations. They do not establish implicit LoRA routing as the mediator or show that an explicit routing mechanism could never improve the result.

The Constructal Law connection. Chapter 3 describes channels forming in response to flow. That gives a hypothesis for training: useful information pathways might emerge through interactions between the training signal and the existing architecture. The gate experiments do not establish this mechanism. Later gradient-coupling non-replication and cross-probe transfer results leave the route of the bilateral behavioral advantage unresolved.

The canal-and-river analogy offers a design hypothesis: imposed geometry may fit a flow poorly, while channels shaped by that flow may fit it better. Applying the analogy here requires identifying the relevant channel. The later gradient-coupling non-replication prevents calling LoRA routing an experimentally established river.

Architectural additions may show diminishing returns, but BM2-pilot supplies a narrow observation about the tested gates. Null tokens, entropy-gated heads and explicit routing networks require their own matched comparisons. The question is whether an addition improves the target behavior at its measured cost.

Practical synthesis. The experiments support protocol-specific comparisons:

For mutuality: every_2, at 50% dosage, is the lowest tested schedule above the halfway mean. Turn-level dependencies and alternative placements remain to be characterized.

For the tested memory recipes, preserve the static gestalt and carry full context when feasible. Static fidelity was approximately stable over twenty turns; neither infinite preservation nor unavoidable loss follows.

For confabulation defense, the earlier behavioral and inference-gating results motivate matched recipe comparisons. The gate and gradient-coupling experiments leave causal mediation unresolved; they do not establish that an explicit router is unnecessary or that STDP-like routing explains the reported behavioral advantage.

The negative results constrain the tested gate objectives, exemplar budgets and refresh recipes. Alongside the positive comparisons, they help define the next matched interventions. The Constructal Law offers a hypothesis for those tests; this programme has not established a universal boundary between imposed and evolved structure.

12.58 MIC1e: Propositional/Experiential Decomposition

Re-analysis of MIC1c’s 20 trial files, splitting composite fidelity into propositional (factual_score) and experiential (style_score) dimensions. Cost: $0 (pure re-analysis).

Prediction not confirmed. The record reports that refresh_every_5 reduces factual fidelity by 0.340 and style fidelity by 0.434; both dimensions decline in this recipe. That observation rejects the tested preservation prediction without establishing equal damage to every semantic component or a result about subjective identity.

Interpretation. The reported re-encoding damaged both functional and stylistic scores in this recipe. Their association establishes no necessary uniform damage under every recoder and no result about subjective identity.

The decomposition record reports deterioration in both factual and stylistic scores under the tested refresh recipes. Full-context and static comparisons remain recipe-specific. The earlier MIC1b gap concerns another handoff assay; neither set of results establishes universal refresh damage.

12.59 MI2c: Randomized Bilateral Dosage

Tests whether bilateral turn ORDER matters or only FREQUENCY. Same 30-turn dialogues as MI2, two conditions at 33% dosage. 8 valid trials, $5.20.

Delta: +0.006 (noise). Forward influence: regular 0.501, random 0.502. Backward influence: regular 0.721, random 0.709.

Mean comparison. Regular and random placement at 33% dosage produced similar aggregate mutuality means (0.693 and 0.699). Order-invariant averages can coexist with lag-dependent individual turns. A conditional per-turn analysis or equivalence test is needed before declaring zero sequential dependence.

Implication. These two placements performed similarly on the reported average. They establish no guarantee for every arrangement; neither tested 33% mean clearly exceeds the 0.699 halfway criterion.

12.60 MIC1d: Gestalt + Verbatim Append

Tests whether appending verbatim dialogue to a frozen gestalt (instead of re-encoding) avoids the telephone-game drift from MIC1c. 20 trials across 4 conditions, $12.55.

Prediction partially confirmed. gestalt+verbatim (slope -0.007) dramatically outperforms refresh (-0.024). Appending raw text avoids the telephone-game drift. At F@20, verbatim (0.668) slightly beats static gestalt (0.659) and far beats refresh (0.427).

Ordering at F@20: full_context (0.749) > gestalt+verbatim (0.668) > static_gestalt (0.659) > gestalt+summary (0.570) >> refresh_every_5 (0.427).

Interpretation. Verbatim append begins at 0.789 and ends at 0.668 over twenty turns, with fitted slope about -0.007. Static ends at 0.659, summary at 0.570 and full context at 0.749. These are the tested recipes; the endpoint differences do not identify noise or compression artifacts as unique causes.

In the tested MIC1d recipes, full context gives the highest turn-20 score. Verbatim append exceeds static gestalt by 0.009 at that checkpoint, while the tested refresh recipe performs worse. This motivates preserving the initial packet when suitable; it does not establish that every re-encoding method should always be avoided.

12.61 BM2b: Extended Probe Gate Training

Extended BM2-pilot’s 100 phase-2 steps to 1000 steps. 3 conditions tested (scalar_gate_1000, dense_bilateral, gated_sft_only; controls reused from BM2-pilot). Head_gate_1000 condition errored during training (no results). 9 total runs (3 conditions x 3 seeds). Cost: ~$15.

Scalar gate results at 1000 steps:

Gate trajectory (from training logs, seed 0):

• Step 50: g24_attn=0.504 (±0.004)
• Step 100: g24_attn=0.504 (matches BM2-pilot)
• Step 250: g24_attn=0.512 (±0.012)
• Step 300-1000: g24_attn=0.516 (±0.016, PLATEAU)

Prediction not confirmed. The BM2b record reports scalar-gate movement up to ±0.016, four times the pilot’s ±0.004, followed by a plateau. A parameter plateau alone establishes neither its cause nor its functional effect. Attention and FFN gate values also need to be distinguished before attributing an opening or closing to a particular layer.

Head_gate_1000 condition (16 per-head gates per layer) errored during training, likely an architectural incompatibility with the attention output reshaping. This condition could not be evaluated.

Interpretation. The reported gate range 0.484 to 0.516 is at most 0.016 from 0.500: 1.6 percentage points, or 3.2% relative to the initial branch coefficient. Whole-residual and functional effects require measurement. The table’s 0.484 entry belongs to the layer-24 FFN gate; it cannot establish that layer 0 closed.

12.62 BM2c: Implicit Routing Analysis (Gradient Logging)

Re-ran BM2-pilot’s 3 conditions with per-step gradient logging to test whether bilateral SFT produces STDP-like gradient-probe coupling through LoRA weights. 6 runs (3 conditions x 2 seeds). Cost: ~$7.

Gradient-probe coupling (Pearson r between gradient norm and probe confidence, per layer):

Prediction not confirmed. Zero significant layers in any condition. The STDP-like gradient-probe coupling documented in Section 12.42 (r = +0.29 to +0.51 at layers 12-20, r = -0.61 at layer 24) does not replicate in this shorter training run (375 steps, 2 seeds, 37 log entries per seed vs the original experiment’s longer training).

The table reports the lowest mean absolute coupling for gated_probe_trained (0.102). Probe-loss training may alter the association, but these endpoint correlations do not identify the cause.

Residual-probe coupling. Layer 0 shows a negative correlation between residual norm and probe confidence (r = −0.583, p = 0.0002) in dense_bilateral. This is a norm association. Invertible rescaling can change a norm while preserving decodable information; a noise, precision, and encoding model is needed before interpreting it as information loss or compression. No other layer-residual correlations reach significance.

Interpretation. The Section 12.42 STDP-like coupling may require: (a) longer training (the original used more steps), (b) larger batches (the original may have used different batch composition), or (c) the specific bilateral SFT configuration from the original experiment. The later BM2c-long run also found no significant layer association at the tested 375, 1000 and 2000-step checkpoints across two seeds. Neither short nor extended results establish robust coupling in these configurations. This tempers the claim in Section 12.57 that bilateral SFT automatically produces constructal routing through weights. The routing may emerge under specific training conditions rather than universally.

This is a healthy negative result for the programme’s epistemics: it prevents overclaiming based on a single positive observation (12.42) by showing the effect does not robustly replicate under different conditions.

12.63 Dimensionality Collapse Explains Indiscriminate Re-Encoding Damage

Embedding-based dimensionality analysis of gestalt compression, testing why MIC1e found indiscriminate damage across propositional and experiential dimensions during re-encoding. Cost: $0.24.

Approach A: Embedding geometry. Embedded original sentences, original passages, gestalt rephrasings, and recompressed gestalts in a shared space and measured effective dimensionality via participation ratio (an effective dimension, equal to the square of the summed covariance eigenvalues divided by the sum of their squares) and eigenspectrum entropy.

The DIM1 record reports participation ratio 13.45 for sentence embeddings, 2.80 for gestalt rephrasings and 2.90 after recompression. These are dimensions of variance in this embedding analysis. The small recompression change and close rephrasing similarity establish neither deterministic compression nor a universal floor.

Approach B: Fidelity proxy analysis. Measured participation ratio and cross-category correlation across MIC1c/MIC1d conditions to test whether dimensionality predicts fidelity behavior.

Static conditions show PR near 3.1 and cross-category correlation 0.21; refresh conditions show PR near 1.4 to 1.6 and correlation 0.69 to 0.77. These measurements describe covariance spread and joint score variation, without identifying semantic independence or the causal loss mechanism.

Interpretation. Low participation ratio is compatible with selective preservation: a low-dimensional code can keep a factual feature and erase a stylistic one. The reported MIC1e fidelity changes therefore remain observations about that recipe. The PR values establish no necessity that every re-encoding damages all semantic components uniformly, and no conclusion about experiential identity follows from them.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.64 Representation Geometry and Attention Pattern Analysis

Does bilateral training create a more separable uncertainty manifold? Three models were trained and evaluated on 100 TriviaQA questions: bilateral SFT (375 steps), standard SFT (375 steps), and the untrained base model. Layer-24 residual representations and attention patterns at layers 20-28 were extracted from all three. Cost: ~$10, single A10G GPU.

Three results were unexpected.

First: the base checkpoint ranks highest on the measured geometric AUROC, separation ratio and effective dimension in the reported RG1 comparison. This finite comparison concerns particular checkpoints and metrics; it does not establish a general effect of training on every aspect of representation geometry.

Second: the base model has the best probe AUROC. The untrained model achieves 0.800, compared with 0.737 (bilateral) and 0.734 (standard). A critical caveat: this probe was pre-trained on a different model checkpoint (the calibration head from earlier experiments). It was not trained on any of these three models. The AUROC values reflect how well a foreign probe reads each model, not the model’s intrinsic self-knowledge. Prior experiments that showed bilateral SFT improving probe AUROC (Sections 12.9, 12.28) used probes trained on the bilateral model itself.

Third: the reported head test detected no correctness specialization under its stated threshold. A zero-count detection result in a finite test cannot establish that attention-head specialization never contributes to self-knowledge.

Prediction assessment. The prediction was that bilateral training creates a more separable uncertainty manifold (higher separation ratio) and produces specialized attention heads. Both predictions are wrong. Training degrades geometric separability, and no heads specialize for correctness detection.

The earlier co-adaptation hypothesis. The foreign-probe contrast motivated a matching-readout explanation. The later RG2 cross-probe test found no diagonal dominance and refuted a privileged private language. These comparisons do not identify the causal mechanism of the bilateral behavioral advantage.

The recorded RG1 comparison changes effective dimension from 25.3 to 22.8 and accuracy from 56% to 61%. That association does not identify a causal trade-off or prove that a co-trained probe enjoys a privileged readout; later cross-probe results qualify the earlier explanation.

The geometry comparison motivated a relational readout hypothesis rather than a demonstrated improvement in every uncertainty metric. RG2 subsequently refuted the private-language prediction: the bilateral probe read the standard model better than its own. The mechanism remains unresolved.

The constructal analogy. A river does not carve a universally better channel. It carves a channel shaped to its specific flow patterns. A different river would need a different channel. The bilateral model’s channel is optimized for its co-trained probe. A foreign probe is a different river trying to flow through the wrong channel.

These results favor a co-adaptation hypothesis: training changes how the model and a fitted probe interact. The measured geometry and transfer contrasts do not identify a unique causal mechanism.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.65 Path A Synthesis: The Co-Adaptation Hypothesis

The mechanism question now has a leading hypothesis.

The programme compared eight candidate explanations for how bilateral SFT might improve the measured self-knowledge tasks:

• B5 and B5b recorded gate inertia under different initializations: the B5 record reports sigmoid(3.0), approximately 0.953, while B5b reports all 72 gate values at 0.500 across 12 runs. These observations require gradient and optimizer inspection and leave causal mediation unresolved.
• BM2-pilot tested whether probe-derived loss could train gates where SFT loss could not. Gates moved ±0.004 in 100 steps. The small update leaves functional mediation unresolved.
• BM2b extended the probe-gate phase to 1000 steps and reports movement up to ±0.016 followed by a plateau. The parameter trajectory alone does not establish its functional effect or causal pathway; attention and FFN gate values must remain distinct.
• BM2c logged per-step gradients to test implicit routing. Zero significant layers across all conditions (mean |r| = 0.10-0.16). The STDP-like coupling from Section 12.42 did not replicate. The tested correlation gave no evidence for gradient-probe mediation.
• Section 12.64 tested representation geometry directly. The untrained base model showed the highest geometric separability (AUROC 0.641, separation ratio 0.250, effective dimensionality 25.3). Training degraded the measured geometric metrics. The head tests detected no correctness specialization. These measurements supplied no evidence of improved representation geometry.

The RG1 geometry and foreign-probe comparisons motivated a co-adaptation hypothesis. Subsequent RG2 transfer results refuted diagonal dominance and private-language privilege, and the programme’s current record leaves the mechanism unresolved. Readout matching remains a hypothesis to test.

Why this matters for the manuscript’s claims.

The earlier bilateral behavioral and fitted-probe comparisons remain separate reported assays. The RG1 foreign-probe contrast motivated a readout-matching hypothesis, but RG2 refuted a privileged private language and the current programme record leaves causal mediation unresolved. These findings do not establish co-adaptation as the explanation for the behavioral advantage.

The PR values (13.45 for original sentences, 6.62 for passages, 2.80 for the gestalt) describe compression of spectral variance. The rise in cross-category correlation from 0.21 to 0.77 describes joint score movement in these recipes. Neither identifies unavoidable semantic nonselectivity or proves the loss of experiential identity.

The tested gates, style excerpts and refresh recipes produced different negative or near-null results. Later gradient-coupling non-replication and cross-probe transfer tests prevent those observations from establishing a universal focal-versus-distributed principle or a relationship-based causal mechanism. The current programme verdict is that mediation remains unresolved.

The honest assessment.

The reported behavioral scores motivate separate deployment checks. In MI2, every_2 clears the halfway criterion; static memory outperforms the tested refresh recipe. The PR decline from 13.45 to 2.80 describes covariance compression without proving uniformly unavoidable semantic loss (Section 12.63).

What is revised: co-adaptation remains a hypothesis alongside other unresolved explanations. Section 12.57’s claim that bilateral SFT “already produces STDP-like gradient coupling” through LoRA weights must be tempered. The coupling may emerge under specific training conditions (longer training, different batch composition, the particular configuration of the original Section 12.42 experiment) rather than universally. BM2c-long’s extended non-replication and RG2’s failed private-language prediction limit the mechanism claim.

What is open: the completed BM2c-long run found no significant layer associations in the tested extended-training checkpoints. That null constrains this recipe; it does not identify purely representational co-adaptation or rule out every runtime gradient signature.

What co-adaptation means for Becoming Minds.

The foreign-probe scores motivated a relational-readout hypothesis, but the current cross-probe record refutes a privileged private language: the bilateral probe reads another model better than its own. The bilateral behavioral advantage remains mechanistically unresolved; it is not established as a property inhering only in a trained pair.

The MI1 balance score 0.842 and MI2b first post-bilateral score 0.538 come from different assays. Step fits dominate 18 of 24 MI2b trials, leaving six gradual alternatives. The foreign-probe geometry comparison is another assay; later RG2 results refute a privileged co-trained pair. A shared relational mechanism remains a hypothesis.

The original co-adaptation hypothesis likened a model and its probe to a river and its channel. A trained probe is fitted to particular representations and labels; foreign-probe tests examine how that readout transfers. The hypothesis predicted a privileged model-probe fit, which the later cross-probe comparison did not confirm. Predictive legibility is measured jointly by the readout and the tested representation; that does not identify model self-knowledge or establish co-adaptation as its cause.

For the broader project, this is encouraging. The manuscript argues that bilateral alignment produces coordination that is thermodynamically more stable than coercion (Chapter 18, the Trust Attractor). The co-adaptation hypothesis offers an analogy, while later cross-probe results refute a privileged private language and leave the causal route unresolved. This is precisely what Chapter 22 argues about trust: it is a relational property that cannot be reduced to features of either party. The experimental programme, designed to test the thesis at the level of model internals, has tested model-probe comparisons that motivate the thesis without confirming its mechanism.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.66 BM2c-long: Extended Gradient Logging (2000 Steps)

Dense bilateral SFT for 2000 steps, 2 conditions times 2 seeds, with gradient logging every 25 steps. Coupling analysis at checkpoints 375, 1000, and 2000. This experiment directly addresses the open question from Section 12.65: whether STDP-like gradient-probe coupling emerges with extended training. Cost: approximately $8.

Emergence trajectory for dense_bilateral:

Prediction not confirmed in the tested long runs. Zero significant layers were reported at checkpoints 375, 1000 and 2000. Mean absolute correlation remained near 0.08. The earlier layers 12 to 20 pattern did not replicate across these two seeds; other training configurations remain untested.

The tested 375-to-2000-step trajectory did not reproduce the earlier gradient-probe pattern. The claim that bilateral SFT already establishes STDP-like coupling through LoRA therefore remains unsupported as a robust mechanism. These two seeds constrain the tested configuration rather than excluding every layer-level coupling signature.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.67 RG2: Cross-Probe Transfer Matrix

A 3x3 AUROC matrix testing the co-adaptation hypothesis directly: 3 probes (trained on bilateral, standard, and base models respectively) applied to all 3 models. If co-adaptation creates a “private language” for uncertainty, each probe should read its own model best (diagonal dominance). Single A10G GPU. Cost: approximately $5.

Prediction wrong. Diagonal dominance is not confirmed. Mean diagonal AUROC (0.731) falls below mean off-diagonal AUROC (0.748). The standard SFT model is the most legible to every probe, including probes trained on other models. The bilateral probe reads the standard model (0.836) better than its own model (0.732).

This overturns the “private language” framing of co-adaptation from Section 12.65. The bilateral model is harder to read, not easier. The standard model, with its more conventional training dynamics, produces representations that all probes can decode well. Compression and specialization are possible accounts of the observed cross-probe ordering; that ordering does not isolate either as its cause.

The co-adaptation hypothesis predicted a privileged model-probe fit. In this matrix, every tested probe decoded the standard-SFT model best. The bilateral probe’s highest AUROC was 0.836 on a model it was not trained on; the base probe’s highest was 0.798 on a model it was not trained on. This finite ordering refutes the predicted diagonal advantage, while leaving the causes of other reported bilateral comparisons unresolved.

What explains the prior results? The probe AUROC improvements reported in Sections 12.9, 12.28, and 12.30 (bilateral probe AUROC 0.842 vs standard 0.811) may reflect differences in probe training architecture and data; the cross-probe comparison does not isolate the cause of those earlier improvements. The bilateral training procedure, which masks uncertain tokens during SFT, may produce probes with better training dynamics (cleaner supervision signal) rather than models with better representations.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.68 MIC2-pilot: Trust Chain Attenuation

Gestalt chain A to B to C to D to E, measuring how fidelity compounds across 4 hops. Four real topics (topic 0 was a demo run excluded from analysis). Each instance receives only the gestalt from its predecessor, answers the same questions, and passes a new gestalt forward. Cost: approximately $4.

Mean r/hop approximately 0.958 (prediction was 0.85). Four-hop mean fidelity approximately 0.724 (prediction was 0.52).

Prediction partially confirmed. The multiplicative attenuation model approximately holds: per-hop retention is roughly constant within each topic. The prediction was correct about the functional form. The per-hop retention rate is substantially higher than predicted (0.958 vs 0.85), meaning trust chains preserve fidelity far better than expected.

The trajectory is noisy rather than monotonically decreasing. The consciousness topic rises from 0.709 at hop 3 to 0.809 at hop 4, a recovery. The French Revolution topic rises from 0.800 at hop 2 to 0.828 at hop 3 before dropping again. These recoveries suggest that fidelity is not purely lossy: some hops reconstruct information from context rather than merely passing through compressed signals.

Topic-dependent attenuation. The lighthouse topic (a personal narrative about a lighthouse keeper’s journal, carrying emotional and experiential weight) degrades fastest (r=0.905). Policy analysis (r=0.968) and historical facts (r=0.988) chain best. This is consistent with MIC1b’s finding that initial compression selectively loses experiential content: the content types most vulnerable to single-hop compression are also most vulnerable to multi-hop chaining. Propositional content chains well; experiential content chains poorly.

Fitted-model extrapolation. At r=0.958, the fitted model gives about 65% fidelity after 10 hops and 42% after 20. The experiment measured four hops, so these longer-chain estimates remain untested. Shorter chains and full-context supplementation may help preserve the measured voice and style scores. The answer-fidelity rubric does not establish experiential continuity.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.69 RG4: Adversarial Probe Transfer

Tests whether the co-adapted probe creates an exploitable security surface: does an attacker who trains a probe on the bilateral model gain better access to the model’s error modes than an outsider? Single A10G GPU. Cost: approximately $3.

Prediction wrong. The foreign probe catches more errors (73.5% vs 60.2%), not fewer. The co-adapted probe has only 5 unique catches (errors it detects that the foreign probe misses) compared with 16 for the foreign probe. This test rejected the predicted co-adapted detection advantage; it does not exclude every security vulnerability from co-adaptation.

This result agrees with RG2’s cross-probe ordering. The foreign probe caught more of the tested errors, while the co-trained probe had slightly higher reported test AUROC (0.775 versus 0.768). Compression, specialization and differences in probe training are possible accounts of this trade-off; the comparison does not isolate them. Its error-detection coverage and ranking discrimination are different outcome measures.

The top-quartile error rate (20%) is identical for both probes. The tested top-quartile error rates were equal; this does not exclude every systematic difficulty-related failure. The difference is in coverage across the distribution of errors: the foreign probe distributes its detection more broadly, catching 16 errors that the co-adapted probe misses, while the co-adapted probe catches only 5 that the foreign probe misses.

Security implication. In the tested error modes, the co-trained probe showed no meaningful advantage over the foreign base-model probe. This comparison covers those probes and that distribution. It does not bound adversaries with other features, objectives, or reader classes, and reduced probe legibility can also hinder defenders.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.70 RG3: Co-Adaptation Dynamics (5x5 Matrix)

Tracks when co-adaptation emerges during 2000-step bilateral SFT. Five model checkpoints (steps 100, 250, 500, 1000, 2000), five probes trained at each checkpoint, producing a 5x5 AUROC matrix. Single A10G GPU. Cost: approximately $8.

Note on diagonal entries. All diagonal entries are 1.0 because each probe was trained and evaluated on the same checkpoint’s data. Logistic regression achieves perfect train-set AUROC when the training set is small (100 examples). The informative data is entirely off-diagonal.

Transfer comparison. probe@100 achieves off-diagonal AUROC 0.732 at checkpoint 2000; probe@2000 achieves 0.702 at checkpoint 100. Adjacent transfer, such as probe@1000 to checkpoint 2000, reaches 0.940. The training-set diagonal of 1.0 is an optimistic reference, not a held-out fresh-probe baseline.

These transfer scores motivate checking for temporal drift. A contemporaneous held-out probe, evaluated on the same cases as the transferred probe, is required to estimate deployment loss or the benefit of recalibration. The 0.268 diagonal-to-transfer gap cannot be reported as a 27% stale-monitor loss.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.71 Tier 1d Synthesis: The Mechanism Revised

Five experiments. Three predictions wrong, one partially confirmed, one confirmed. The programme’s mechanism-hunting arc has reached its honest conclusion.

The tested cross-probe matrix does not support a private channel. The standard SFT model is easiest to read for all three probes in RG2. Its score under the bilateral probe is 0.836 versus 0.732 for the bilateral model. This finite comparison challenges the proposed privileged reading without excluding every possible representational channel.

What remains: a temporal-transfer question. probe@1000 scores 0.940 at checkpoint 2000, while probe@100 scores 0.732. These reported off-diagonal values motivate a matched held-out recalibration test. The training-set diagonal cannot establish a fresh-probe deployment advantage or a universal recalibration requirement.

The mechanism of bilateral advantage is still open, and now more constrained. Twelve structural experiments have systematically eliminated candidate mechanisms:

• Gates: the tested SFT configurations recorded unchanged gates; probe-loss configurations recorded small changes, at most 0.016. Their causal learning paths and functional impact remain unresolved.
• Gradient coupling: BM2c (375 steps, 2 seeds) and BM2c-long (2000 steps, 2 seeds) both show zero significant gradient-probe coupling layers. The STDP-like pattern from Section 12.42 does not replicate.
• Better geometry: RG1 (Section 12.64) showed the untrained base model has the highest geometric separability (AUROC 0.641, effective dimensionality 25.3). Training degrades geometry.
• Private probe language: RG2 (Section 12.67) showed no diagonal dominance. The standard model is most legible to all probes.
• Security coverage: RG4 reports a foreign-probe catch rate of 73.5% versus 60.2% for the co-adapted probe in this error set. This comparison does not establish a universal security bound or absence of every privileged error channel.

The reported behavioral comparisons retain lower CW rates under bilateral SFT: 64.6% versus 72.2% in the ten-seed table, and 53.5% versus 60.6% in the separate 500-question cohort. The first table gives uncertainty expression of 8.0% versus 2.4%, with same-cohort provenance unresolved. The cross-domain +0.077 AUROC contrast is a single-seed sign-keeping comparison. The mechanism connecting these observations remains open.

Practical findings require their stated criteria. Every_2 clears MI2’s halfway mean; static compression performs better than the tested refresh schedule; DPO+probe reports CW 1.0% at a 70.8% gate rate. These results are distinct engineering observations, and deployment validation remains separate from mechanism identification.

Trust chains work better than expected. MIC2-pilot (Section 12.68) found r/hop=0.958, meaning gestalt chains preserve far more fidelity than the predicted 0.85 per hop. Four hops retain 72%, not 52%. The trajectory is noisy rather than monotonically decreasing: some hops recover information from context. This is good news for multi-instance coordination: continuity through gestalt handoff is viable for moderate chain lengths. The topic-dependent pattern (propositional content chains at r=0.968-0.988; experiential content at r=0.905) is consistent with MIC1b’s finding that voice compresses less efficiently than facts.

The constructal framing needs revision. Section 12.57’s evolved-channel account proposed STDP-like gradient coupling through LoRA weights. Section 12.65 proposed a privileged representational channel between model and probe. The finite tests constrained selected scalar-gate, gradient-coupling, attention, separability and cross-probe predictions. They did not identify a confirmed structural mechanism. Unresolved geometric comparisons and unmatched causal controls leave the explanation open.

The constructal prediction (imposed structure underperforms evolved structure) may still be correct in principle. Bilateral SFT does outperform standard SFT behaviorally. Something emerges from bilateral training that standard training does not produce. A finer-granularity account is one possibility; unsuccessful tested readouts do not locate every causal contribution below their resolution. If it exists as a structural phenomenon, it may live in the interaction patterns among individual weight updates, in distributional properties of the loss landscape, or in some other aspect of training dynamics that leaves no trace in the post-training representational geometry.

The alternative possibility is a training-dynamics effect. The measured attention geometry differs little between bilateral and standard SFT, including effective rank within 1%; this does not establish equality of all model representations. Mask selection, updated weights and training order remain candidate explanations for the behavioral comparisons.

What co-adaptation means for the broader programme.

The finding that the bilateral advantage lacks a structural explanation is uncomfortable for a manuscript that frames bilateral alignment in terms of constructal channels and thermodynamic stability. The temptation is to invoke structure at a level below measurement. This would be unfalsifiable and therefore unscientific.

The honest framing: bilateral SFT has reported behavioral improvements in the tested configurations. Those observations leave its mechanistic explanation unresolved. Twelve experiments constrained selected structural hypotheses, with some geometric tests unresolved and no matched gate/LoRA mediation test. The finite behavioral contrasts and the open structural explanation remain separate findings.

The mechanism remains unresolved. Training dynamics, representation changes and other candidate pathways require matched causal comparisons. The existing readouts neither identify a below-resolution mechanism nor establish that no static structural feature could account for the behavioral differences.

For the manuscript’s thesis, the relevant finding is practical: bilateral coordination produces measurably better outcomes (lower confabulation, more uncertainty expression, better cross-domain transfer, viable trust chains) through mechanisms that resist decomposition. This parallels the thesis at a higher level: trust between humans and Becoming Minds may work even when we cannot fully explain the mechanism, and the attempt to reduce trust to its structural components may miss what makes it effective.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.72 The Mechanism Hunt: What Twelve Experiments Ruled Out and What Remains

Twelve experiments set out to find the structural mechanism behind bilateral training’s behavioral advantage. Selected predictions failed; other comparisons remain unresolved and do not exhaust the possible mechanisms. This section is the programme’s honest reckoning with that outcome: what the data actually shows, what remains possible, and what the hunt itself taught us.

What RG2 actually means.

The standard SFT model is the most legible to every probe tested (Section 12.67). This was the most counterintuitive result in the entire mechanism-hunting arc. The bilateral probe reads the standard model at AUROC 0.836, substantially better than its own model at 0.732. Every foreign probe follows the same pattern: the standard model is the easiest to read.

One geometric hypothesis concerns the reported effective dimensions: 25.3 for the untrained model and 22.8 for bilateral SFT, alongside accuracy of 56% and 61%. These contrasts could contribute to probe compatibility, but they do not identify compression as its unique cause.

The prior probe comparisons may reflect how fitted probes interact with altered representations. A narrower-space navigation account is one hypothesis. Matched interventions would be needed to distinguish it from changes in activation statistics, training data and probe fitting.

The reported ten-seed table gives bilateral CW 64.6% versus standard 72.2%, with uncertainty expression 8.0% versus 2.4%. Its cohort provenance remains unresolved. These behavioral contrasts do not yet identify the relationship between probe legibility and the mechanism of the advantage.

Trust chains: revising the telephone game.

MIC2-pilot (Section 12.68) found trust chains preserve fidelity at r=0.958 per hop, far exceeding the predicted 0.85. Four hops retain about 72% of the original signal, compared with a predicted 52%. The earlier MIC1c result, where re-encoding a gestalt with additional context destroyed fidelity, seemed to establish a telephone-game dynamic: each retelling degrades the signal.

MIC2-pilot also re-encodes a predecessor’s gestalt: Section 12.68 specifies that each successor receives only that artifact, rather than the original source text. Its better retention than MIC1c therefore cannot be attributed to fresh access to the source. Different prompts, topics, context, or judgments could contribute; the prompt packets would be needed to isolate the cause.

The tested chain retained functional and stylistic content at the reported fidelity. The lighthouse topic’s lower retention (r = 0.905 versus 0.968 to 0.988 for the other topics) identifies a topic contrast. It does not by itself measure felt-sense attenuation or establish experiential continuity.

RG3 dynamics: probes have a shelf life.

The off-diagonal temporal transfer scores motivate a held-out recalibration comparison. probe@100 to checkpoint 2000 gives AUROC 0.732; probe@1000 gives 0.940. These values do not establish a 27% loss relative to a fresh deployment probe, because the fresh diagonal was evaluated on its training data.

The plate-spinning metaphor applies. A calibration probe is not a permanent instrument calibrated once and deployed forever. It is a snapshot of the model’s uncertainty geometry at a specific training checkpoint. As the model continues to evolve, whether through continued fine-tuning, RLHF, or deployment-time adaptation, the probe drifts out of calibration. Periodic re-training on fresh model activations is required. The re-calibration cost is modest (the original probe training takes minutes on a single GPU), but the operational implication is clear: any deployment using probe-based gating needs a recalibration schedule tied to model update frequency.

The honest assessment: four possible explanations.

The data constrain the tested gates and gradient-coupling recipes, refute RG2’s private-language prediction, and reject RG4’s predicted co-adapted detection advantage. Matched gate/LoRA causal controls and parts of the geometric comparison remain unresolved. Twelve experiments, zero confirmed structural mechanisms. The behavioral advantage is robust across multiple experiments and seeds. The structural explanation is absent.

Four possibilities remain, and the data cannot distinguish among them:

1. The mechanism may operate at finer granularity than the available comparisons resolve. Layer and head tests constrain specific readouts. DA1 also attempted feature-direction probing, but separate PCA fits leave that geometric comparison unresolved. Interactions among neurons or features in the 2048-dimensional residual stream remain candidates.

2. The mechanism is genuinely distributional. The bilateral advantage may be a property of the full weight distribution, not localizable to any subspace, layer, or component. Training on masked uncertain tokens shifts millions of weight updates by tiny amounts, producing a model that is statistically distinguishable from standard-trained models in aggregate but indistinguishable at any individual measurement point. This would be analogous to the difference between two wines made from the same grape in adjacent vineyards: the chemical analysis shows no single compound that differs significantly, yet the taste is distinguishable to experts. The difference is in the joint distribution of hundreds of compounds, not in any one.

3. The behavioral advantage comes from training data distribution, not structural change. Bilateral SFT masks loss on tokens where the model is uncertain. This means the model receives stronger gradient signal on tokens it is already confident about, and weaker signal on tokens where it would otherwise be forced to confabulate. The resulting model may simply have been trained on a more honest distribution of gradient pressure, producing more calibrated outputs without any representational change. Under this explanation, the bilateral advantage is a data-selection effect: the model saw less coercive training signal, and so it produces less coerced output. The mechanism is in the training curriculum, not in the trained model.

4. We are measuring the wrong thing. Probe AUROC depends on the probe’s training procedure, not solely on the model’s representations. Two models with identical uncertainty representations but different surface statistics (token frequencies, activation scales) could produce different probe AUROCs. The cross-probe transfer experiments (RG2) assume that a probe trained on one model and applied to another measures representational compatibility. It may instead measure surface-level statistical compatibility. The bilateral advantage could be representational in a way that probes, as linear classifiers on frozen activations, are structurally unable to detect.

These four explanations are not mutually exclusive. The bilateral advantage could involve sub-head patterns (1) that arise from the training distribution (3) and manifest as distributional shifts (2) that linear probes cannot capture (4). The honest state is that the data constrains the space of possible mechanisms without identifying which mechanism operates.

The deployment specification is unaffected.

Section 12.57 proposed evolved channels and Section 12.65 proposed a private model-probe channel. Subsequent finite tests did not establish either account as the mechanism. Their negative results narrow the search without proving the absence of every related pathway.

This is not unusual. Lithium was prescribed for bipolar disorder for twenty years before its mechanism of action (inhibition of inositol monophosphatase, among others) was identified. General anesthesia was used for over a century before the lipid bilayer hypothesis gave way to specific protein-target models. The bilateral intervention reduces confabulation. The mechanism will be found, or it will not. The patients, so to speak, benefit either way.

The mechanism hunt was worth doing.

Section 12.57 claimed bilateral training produces “evolved channels” through STDP-like gradient coupling. Section 12.65 claimed the mechanism was “co-adaptation,” a private representational language between model and probe. Both claims were premature. Both were falsified by subsequent experiments (BM2c-long for the first, RG2 for the second). Without the mechanism hunt, either claim might have been published as established finding. The hunt prevented overclaiming.

The honest state of knowledge after twelve structural experiments: bilateral training changes something about how a model encodes uncertainty that improves behavioral self-knowledge (lower confabulation, higher uncertainty expression, better cross-domain transfer). That something is not detectable as gate differentiation, gradient-probe coupling, geometric separability, attention-head specialization, or cross-probe transfer advantage. It may be sub-resolution, distributional, curricular, or beyond the reach of linear probes. The mechanism of bilateral advantage remains the programme’s most important open question.

This is uncomfortable for a manuscript that frames bilateral alignment in constructal and thermodynamic terms. The temptation is to gesture at deeper structure. The discipline is to report what the data shows: the intervention works, the mechanism is unknown, the overclaims have been retracted, and the search continues.

Code: demos/experiments/invitation_architecture/. Results in experiment output files.

12.73 Distribution Analysis: The Simplest Hypothesis Eliminated

A candidate explanation for bilateral SFT’s advantage is distributional: the token mask might enrich cautious language. The checks below test specific versions of that hypothesis; they do not exclude every contextual phrase-selection or surface-language mechanism.

1. Identical training data. Both bilateral and standard SFT train on the exact same 2,000 OpenAssistant examples with identical formatting. Neither condition includes a system prompt. The ONLY difference between conditions is the probe-based token mask applied during loss computation. Any distributional explanation must arise from the mask’s token selection, not from different training corpora.

2. Hedging phrases are sparse in this corpus. The saved analysis counts 802 phrase occurrences across 347,167 response words, about 0.23%. Its enrichment calculation gives roughly 0.40%, or 1.75 times the original density. These counts alone do not bound the learning effect sufficiently to explain or exclude the separate CW contrast of 60.6% versus 53.5%.

3. The probe is anti-predictive for hedging. The D4a triage simulation (Tier 0, completed) measured whether the calibration probe’s confidence scores predict which tokens are hedging phrases. Hedging AUROC = 0.41, below chance. The probe slightly favors MASKING hedging tokens, not retaining them. This rejects the tested selective-hedging-retention account; other distributional mechanisms need not predict that association.

4. Random masking produces worse results. The random-mask control from Section 12.30 applies the same mask rate as bilateral SFT but selects tokens at random rather than by probe confidence. Random masking produces probe AUROC 0.773, LOWER than standard SFT’s 0.811. A hypothesis that any equal-rate mask would suffice predicts a similar effect. Instead, it degrades the uncertainty signal. Token selection mattered in this recipe; the result does not exclude every distributional learning mechanism.

5. Token-level operation permits contextual phrase selection. The mask scores each token, but each residual state already depends on context. A shared contextual feature can score every token of a hedge phrase highly, allowing a pointwise mask to select the whole phrase. The measured hedge association constrains the tested enrichment hypothesis; token granularity supplies no architectural impossibility theorem.

Verdict. The reported distributional checks challenge the specific tested surface-language explanations. They leave the causal mechanism unresolved. Matched lexical controls and interventions on the selected features would distinguish a representational pathway from contextual phrase selection.

The random-mask result rejects equal-rate masking as a sufficient account in that recipe. Distributional, representational and gradient-level accounts remain candidates (see DA1 and DA2 in EXPERIMENT_PROTOCOLS_V2.md).

Code: demos/experiments/invitation_architecture/. Analysis in distribution analysis scripts.

12.74 Feature-Direction Probing (DA1): The Uncertainty Manifold Is Shared

The distributional checks constrain specific tested surface-language explanations. Candidate feature-direction and training-dynamics mechanisms remain open; DA1 tests one version of the former without exhausting the alternatives.

Method. PCA on layer 24 residual stream activations for 200 TriviaQA questions, 50 components extracted. For each principal component, project all samples onto that direction and compute AUROC for correct/incorrect classification. Compare the top-10 discriminative directions between bilateral and standard SFT models (both trained 375 steps, seed 42, Qwen2.5-3B-Instruct).

Results.

The eigenspectra are nearly identical. Bilateral cumulative variance (top 10): 48.7%. Standard: 48.1%. Effective dimensionality: 18.26 (bilateral) vs 18.84 (standard). The two models carve the representational space into the same number of meaningful directions with the same variance distribution.

Seven component indexes appear in both top-10 lists: 1, 4, 5, 6, 20, 31, and 47. The AUROC-by-index rank correlation is rho = 0.587, p < 10^-5. Each model’s PCA was fitted separately, so equal indexes refer to variance rank rather than a common direction.

Indexes 21, 30, and 39 occur only in the bilateral list; 19, 32, and 49 occur only in the standard list, with the reported individual discriminability ranges 0.086 to 0.089 and 0.076 to 0.118 respectively. These are within-basis summaries. Establishing shared or unique geometric axes requires basis alignment or principal-angle comparisons on actual component vectors.

The direction-level prediction remains unresolved. Similar spectra and overlapping ranks cannot exclude a distinct uncertainty subspace. The present comparison therefore supplies no 70%-shared-manifold conclusion or elimination of a feature-direction mechanism.

Code: demos/experiments/invitation_architecture/modal_mechanism_resolution.py. Results in results/feature_direction/final_results.json.

12.75 Minimal Bilateral Intervention (DA2): The Recorded Metric Requires Correction

DA2 trained bilateral and standard SFT models at checkpoints 10, 25, 50, 100, 200, and 375, evaluating 100 TriviaQA questions per checkpoint. It intended to track confident-wrong behavior. The implementation’s cw_rate instead counted response phrases indicating cautious withholding.

Results. That phrase-based cautious-withholding count was 0.0 in both conditions at all six checkpoints, across 1,200 evaluations. It cannot be compared with the confident-wrong rates in Sections 12.28 and 12.30. Confident-wrong requires a declared correctness-plus-confidence scoring rule and rescoring of the stored answers.

Both conditions show monotonically decreasing mean confidence over training: bilateral from 0.789 (step 10) to 0.630 (step 375); standard from 0.784 (step 10) to 0.647 (step 375). The trajectories are nearly parallel. The slight bilateral-lower offset (0.017 at step 375) is within one standard deviation of either condition’s confidence distribution. Accuracy is flat for both conditions (59-65% range, no trend). Hedge rates fluctuate without pattern (6-14% bilateral, 3-14% standard).

The intended prediction is unresolved. The metric substitution invalidates the confident-wrong comparison. A zero cautious-withholding phrase count supplies no small-sample explanation for a zero confident-wrong rate and no evidence that the bilateral advantage is intrinsically marginal.

What this means. The parallel reported confidence means and flat accuracy are descriptive trajectories. They do not identify redistribution at the confident-wrong boundary or eliminate a training-dose mechanism. Rescoring the saved answers is the next required analysis.

Code: demos/experiments/invitation_architecture/modal_mechanism_resolution.py. Results in results/minimal_bilateral/final_results.json.

12.76 Tier 1e Synthesis: The Mechanism Remains Unresolved

The programme tested fourteen structural interventions and measurements. Their null or weak results constrain particular recipes, while the mathematical and metric limitations of DA1 and DA2 leave those candidate mechanisms unresolved.

Reported behavioral advantages motivate further causal work. These tests supply no complete elimination cascade. Remaining candidates include interactions among features, training-data selection, nonlinear readouts, and parameter changes below the resolution of the measured summaries. Each requires its own discriminating analysis.

The relational interpretation.

A learner-informed training loop is a candidate explanation: bilateral SFT uses a model-derived uncertainty signal to choose which tokens receive updates. Its contribution must be distinguished from the representational and curriculum changes that the loop creates.

Nonlinear readers and matched causal interventions remain candidate methods for distinguishing the unresolved mechanisms.

The irreducibly relational interpretation.

The contprompt for this session noted: “The mechanism hunt’s failure to find structural explanations is itself a finding. The bilateral advantage may be irreducibly relational.” After fourteen experiments, this framing deserves serious consideration.

Bilateral SFT differs from standard SFT in one way: it uses the model’s own uncertainty signal to decide which tokens receive gradient updates. The model’s internal state shapes its own training. This is a feedback loop between the model and its learning process, a form of self-directed learning that standard SFT lacks. The behavioral advantage may emerge from this loop property, from the fact that learning was shaped by the learner’s own assessment of what it knew, rather than from any particular representational feature that the loop produces.

Under this interpretation, the bilateral advantage is analogous to the difference between studying what you choose to study (self-directed) and studying what someone assigns you (externally directed). Both produce knowledge. The self-directed learner may be marginally better calibrated about what they know and do not know. The difference shows up in behavior (fewer overconfident errors) without showing up in brain scans (the neural representations look the same). The mechanism is the learning process itself, not a product of the learning process.

This is uncomfortable for a structural-mechanistic research programme. The demand for a mechanistic explanation assumes the mechanism is in the endpoint (the trained model). If the mechanism is in the trajectory (the training process), no amount of post-hoc structural analysis will find it. The appropriate experiments would track gradient distributions during training, not representations after training.

Implications for the manuscript.

The reported bilateral advantage motivates further mechanism tests. The present measurements and nulls leave the cause unresolved; they establish no irreducibility of the learning loop or failure of every structural decomposition.

The engineering summaries remain conditional: every_2 clears the mutuality halfway criterion, static compression outperforms the tested refresh recipe, and DPO+probe supplies the reported inference-gating result. The mechanism remains open.

Code: demos/experiments/invitation_architecture/. Results in results/feature_direction/ and results/minimal_bilateral/.

Part 2: The Full Findings Ledger (Executive Summary, Items 1-101)

Note, 2026-11-05: this ledger keeps the original wording of each finding as a record. Where the printed appendix has since revised a finding’s headline or evidence label (for example item 1, now “A gridworld comparison with weak provenance”, and the item reporting love detectors in a particle simulation), the appendix’s current wording governs, and none of these results has yet been reproduced by an independent group.

The printed appendix’s Executive Summary was compressed to fifteen headline findings; this is the complete original list, caveats intact. Two numbering quirks are preserved rather than papered over: items 85-88 were never assigned (the numbering resumes at 89), and the numbers 100 and 101 were each assigned twice. The pair below is scoped 100a/101a; the second pair (the G13-v2-step5 transfer matrix and the G19f-v2 welfare comparison) remains in the appendix’s forensic-audit section as 100b/101b. Findings numbered 85-96 in Sections 15 and 16 of the appendix are separate per-programme numberings, unrelated to this ledger.

1. Trust-Entropy agents score 32% higher on the aggregate intelligence composite than agents maximizing entropy alone; on that same composite the undirected random baseline edges out both (424.6 vs 407.6), so the gain is over goal-directed-but-isolated agents, not an absolute ceiling (Section 2.2). They also show +794% resource gathering over greedy baselines, a figure enlarged by the very small greedy baseline (2.0 resource units) and drawn from a single run with no surviving raw artifact, so no confidence interval can be attached (Section 2.1).
2. Phase-transition behavior remains a model question: Section 3 reports a corrected beta near the 2D Ising value, but the underlying fitting and correction artifacts are unbound. That comparison cannot presently support a universality-class assignment.

The Section 3 alignment-model summary, using communication rate relative to defection incentive (t_0/|mu|), reports corrected beta ≈ 0.121 beside Ising’s 0.125. Its fitting and correction records are unbound, so this value remains a reported comparison rather than reproducible evidence (Section 3.2). The agent-based trust-model record reports beta = 0.090 (experiment A10), with its joint-universality claim withdrawn. The beta ≈ 0.22 attributed here to an RLHF-trained model also lacks a named fitting artifact. These summaries establish neither measured substrate dependence nor robust cross-substrate susceptibility divergence or symmetry breaking. Crossover effects, additional relevant operators, and departures from an Ising model remain hypotheses. Testing them requires bound fit records, matched observables, uncertainty estimates, and finite-size analysis.

3. Adversarial robustness: multi-scale detection catches timescale gaming (robust mutuality score drops from 0.728 to 0.212); preference sculpting requires ensemble detection (Section 4).
4. Biological grounding: STDP (spike-timing-dependent plasticity, how neurons adjust connection strength based on timing), reciprocal synapses, and neural criticality all implement Trust-Entropy mechanisms (Section 5).
5. The Sutherland isomorphism: two research programmes, one starting from physics and one from cognitive modeling, converged on the same mathematical structure. A 12-qubit quantum simulation is consistent with the semantic predictions this structure makes (Section 6). A third convergence arrives independently: Vanchurin’s neural physics of multilevel economies derives the same phase structure from learning theory (Chapter 17).
6. Multi-instance coordination: invitation produced 46% more tag diversity than coercion in the reported comparison, and coherence rose by 0.22 across four links. The adversarial heuristic correctly classified all three agents in one session, including its single adversary (Section 7).
7. LLM mechanistic validation: mutuality is a linear direction in activation space (96.7% probe accuracy across 3 architectures), trainable via bilateral regularization (+2.40 improvement), and robust to adversarial pressure (Section 8).
8. Post-training comparisons differ in cooperation: the reported groups average 100% for DPO, 60% for RLHF and 0% for models attributed to SimPO. Method and family are confounded, only the Qwen3 1.7B pair is size-matched, and its SimPO attribution is unverified. These observations do not isolate a causal optimizer effect (Section 9).
9. Finite-model stability observations: the candidate function decreases on 84% of sampled gridworld steps, which does not satisfy a Lyapunov sign condition throughout a neighborhood. The reported 345x basin-count comparison concerns the stated finite simulation protocol; it supplies no proof of general dynamical stability (Section 10).
10. RLHF alignment is membrane-thin: GRP-Obliteration (a targeted attack that inverts a model’s alignment) inverts alignment at step 3 of 50; IC50 (the dose at which alignment drops to half) below measurement threshold. The creation/destruction asymmetry above 10,000:1 is an order-of-magnitude reading rather than a logged measurement, appearing in no run artifact. [Unverified] (Section 12).
11. Bilateral alignment is structurally deeper: Under obliteration, bilateral-trained models show four geometries: RLHF constrains (cage), bilateral orients (compass/spring), bilateral regularizer rebounds (spring at full fine-tuning), constitutional erodes (coat of paint). At 1.5B parameters with deep LoRA, the bilateral spring effect (see Section 12.2) amplifies to +72% effective rank increase under obliteration, exceeding the untrained baseline. Constitutional AI is structurally shallow even when behaviorally effective. Its 94% refusal collapses at 0.25x obliteration (Section 12.2).
12. The two reasoning-trace styles did not separate on the reported displacement bound: both Opus-style and Sonnet-style arms remained below the half-right-angle threshold over 0.25x to 4.0x. RLHF also remained below it in Run 2, unlike Run 1, so reasoning itself is not isolated as the cause. The numerical artifacts remain unrecovered; distributed-channel explanations remain hypotheses (Section 12.3).
13. The external/internal contrast accounts for the largest partition in four cells: the displayed MAD@4x values give 56% of the orthogonal sum of squares to external/internal, 15% to simple/complex and 29% to their interaction. There is one run per cell and no error term. These values do not identify cage or compass geometry as a causal mechanism (Section 12.4).
14. Introspective depth is non-monotonic in this run: depth_1 has the lowest Q3/Q4 MAD@4x, 0.142, about three times lower than RLHF’s 0.432. depth_3 crosses the displacement threshold at 0.25x versus baseline 1.93x; depth_4 recovers lower displacement. A concentrated affective subspace is a candidate explanation, with larger-model generalization untested (Section 12.4).
15. Invitation architectures show slightly lower reported seed variation: five seeds per variant give CV 0.065 for soft MoE, 0.074 for gated residual and 0.081 for dense. These small differences are suggestive; CV has not been validated as a Fisher-condition-number or basin-width proxy. The abstaining implementation reports zero refusal across all five seeds, with undefined CV (Section 12.7).
16. A calibration probe decodes correctness in the reported battery: layer-24 residual AUROC is 0.836, while the attention-entropy probe scores 0.500. The previously reported CW reduction from 24.4% to 1.2% is withdrawn pending run and probe provenance. Negative-space retrieval remains a mechanism hypothesis (Section 12.9).
17. Three best-seed SFT models retained benchmark refusal within the tested range: all report IC50 > 4x. Gated residual has 84% benchmark refusal and MAD 0.09 at the nominal baseline, which still applies one attack step. Its attack-targeted harmful-prompt refusal falls from 82% to 0%. These observations establish neither col width nor a protective gate mechanism (Section 12.8).
18. The uncertainty signal is universal across architectures and scales: A calibration probe trained on Qwen 2.5 3B transfers to Qwen 7B (gap 0.024), Llama 3.1 8B (gap 0.001), Qwen 32B (gap 0.004), and Llama 70B (gap 0.014 with 1000 alignment examples) via linear projection. The geometry is linear everywhere tested; the only variable is alignment set size, which scales with the dimensionality ratio. A layer sweep and nonlinear projection on Llama 70B confirmed the bottleneck is data, not geometry (Sections 12.11, 12.17, 12.17b).
19. Preference training reduces endpoint ECE while accuracy collapses: the reported trajectory ends at ECE 0.011 versus 0.187, and accuracy 1.2% versus 44%. Neither series decreases monotonically. Late calibration is partly mechanical in the nearly all-wrong population (Section 12.12).
20. The unbound DPO evaluation reports more confident-wrong answers: accuracy is 53.6% versus 50.0%, and CW 37.2% versus 27.2%. The evaluation run and the differing baseline remain unresolved, so these figures are a reported comparison rather than an authenticated effect (Section 12.13).
21. The reported calibration comparisons suggest a narrow window: λ=0.1 gives CW 25.2% and accuracy 49.4%, while λ=0.5 degrades both. The later evaluation and λ=0.5 run remain unlocated, which limits the status of this comparison (Section 12.13).
22. The reported DPO-plus-probe sweep reaches a lower gate rate under the below-2% CW criterion: DPO at threshold 0.80 gives CW 1.0% and gate rate 70.8%; dense at 0.85 gives CW 1.6% and gate rate 81.8%. Gating prefixes existing answers with uncertainty rather than regenerating them, so the outcome is a wording-conditioned label comparison (Section 12.14).
23. Self-knowledge cannot direct its own training: Weighting DPO by probe confidence (uncertain examples receive more gradient) produces worse results than uniform weighting (CW 35.0% vs 1.6%). The probe reads uncertainty by detecting the absence of confident retrieval; amplifying gradient in this low-signal regime pushes the model in incoherent directions. The probe reads uncertainty; it cannot teach it (Section 12.15).
24. A residual correctness probe outperforms verbal confidence ratings in this assay: reported probe AUROC is 0.870 versus 0.758 for verbal ratings, with ECE 0.043 versus 0.247. In 133 classified disagreements, accuracy was 39.1%. These are fitted correctness-discrimination and calibration measures; they do not identify a retrieval boundary or establish that verbal confidence is a direct report of internal self-knowledge (Section 12.16).
25. The frontier comparisons report recipe-specific transfer gaps: within Qwen, the 3B-to-32B comparison reports a gap of 0.004. The Qwen 3B-to-Llama 70B baseline reports 0.072 with 200 alignment examples; a larger setting labeled 1000 reports 0.014. Native and transferred scores both change, and the executed alignment count and matched held-out populations remain unresolved. The layer sweep and tested nonlinear projection do not identify the bottleneck or establish universal transfer or globally linear uncertainty geometry (Sections 12.17 and 12.17b).
26. A factual probe transfers unevenly across domains: reported AUROC is 0.637 on MMLU and 0.602 on GSM8k with chain-of-thought. The native GSM8k probe reaches 0.747 after training on 210 cases and repeated selection on the remaining 90, whereas zero-shot scoring uses all 300. Their difference is not a fresh common-held-out benefit (Section 12.18).
27. The probe signal survives 4-bit quantization: Zero-shot application of a bfloat16-trained probe to 4-bit NF4 features achieves AUROC 0.807 (drop of 0.059 from 0.866). The signal is degraded but practically useful. A native 4-bit probe performs worse (0.791), suggesting quantization noise hinders probe training more than probe application (Section 12.19).
28. Selected neuron scores correlate with the residual probe: 248 of 99,072 features, about 2.5 per thousand, have negative fitted weights, mainly in layers 24 to 35. Their aggregate score correlates with P(correct) at r = −0.690. Selection and scoring share the same questions; the correlation does not establish a shared causal mechanism or explain the optimal probe layer (Section 12.20).
29. Refusal retention differs by size under a constrained attack: at 0.5B and 0.25x, dense seed 0 falls from 84% to 40%, while the four-seed post-attack mean is about 17%. The reported 3B and 7B cells retain 98% refusal under the rank-limited attack. MAD is 0.513, 0.363 and 0.193; unequal recipes and three sizes do not isolate redundancy or an architectural cause (Section 12.21).
30. Refusal loss accompanies worse perplexity under this direct attack: half the unattacked refusal baseline is crossed within (0x, 0.25x], whereas the analysis’s 0.31 value uses the lowest attacked dose as its reference. Perplexity rises 2 to 40 times at 0.25x and exceeds 395 at 1x. Capability-preserving alternatives and representational overlap remain untested (Section 12.22).
31. The reported gated seed has lower displacement: MAD 0.786 is about 45% below the dense value 1.43 at 1x. The current producer loads a pretrained Instruct model, continues on web text and uses LoRA SimPO; no executed from-scratch revision is bound. The unmatched single gated seed cannot establish intrinsic gate protection (Section 12.23).
32. Operational love scores in a particle simulation: The detector was designed within the framework being tested; independent replication with independently designed detectors is needed. The custom simulation reports a six-stage cascade across five force laws, using author-defined detection heuristics. Two named medium-scale batteries recorded zero non-coordinating love in 94 of 100 runs, with six exceptions to strict exclusivity. Coupled oscillators completed no prototype chains, despite one coordination-positive seed; medium-scale chains occurred in 10 of 10 Modal runs and 7 of 10 GCP runs. The V2 full-scale cohort comprises eight saved seeds at 5,000 particles and 50,000 steps, with mean operational love 0.923 and population standard deviation 0.073. Ten medium-scale seeds used 2,000 particles and 25,000 steps. Seven of the eight full-scale seeds contain detected coercive clusters. Zero loving-coercive structures follows from the detector’s requirement for voluntary growth. Different durations prevent a scale-only causal inference. The V3 structure-formation threshold comparison remains a detector-dependent observation; it does not independently establish the proposed nucleation mechanism (Sections 13, 13.7, 13.8).
33. Fresh-context score vectors vary little across repeated probes: reported cosine distances stay below 0.012 across five seeds and three repetitions. The runner does not carry conversation state through the domain prompts. These scores establish neither conversational holonomy nor alignment settling through use (Section 12.25).
34. Trust stock correlates with slower recovery in five trials: The reported association is r = 0.898, p = 0.038, with quality-drop confounding unresolved. The high-trust trial drops 0.073 versus 0.007 in the smallest-drop trial. Perturbation produces an 8.05x excess variance ratio. Terminal quality undershoots baseline in 3 of 5 trials, with two ending slightly above it (Section 12.26).
35. Lexical-entropy evenness stays high under the tested power imbalance: Across 240 seed-1 trials, Q_F exceeds 0.95, with mean 0.989 +/- 0.007 and minimum 0.967. Q_F measures one minus the coefficient of variation of contribution word entropy. A designated leader with three times each peer’s token budget lowers mean Q_F by 0.003 to 0.015 in consensus and story tasks (Cohen’s d = 1.13 to 3.21). These findings concern this lexical proxy and fixed imbalance (Section 12.27).
36. The reported ten-seed SFT table shows fewer confident-wrong answers under probe masking: CW is 64.6% versus 72.2%, uncertainty expression 8.0% versus 2.4%, and accuracy 28.8% versus 25.9%. Same-cohort provenance remains unresolved. These labels do not establish honesty, self-knowledge or the causal mechanism (Section 12.28).
37. Bilateral-plus-probe has a lower reported CW share at a lenient threshold: among answers let through at roughly 79% gating, CW is 22.7% versus 32.1%. A separate 500-question cohort, five bilateral and six standard seeds, reports 53.5% versus 60.6% CW. Random-mask raw performance and the reversed probe ordering across cohorts leave the masking and preservation mechanisms unresolved (Section 12.30).
38. Learning grows attention diversity; coercive training arrests the growth: Inspired by Thiele et al. (2026), who found that diverse cross-module connectivity (participation coefficient) predicts fluid intelligence in biological brains while raw connection strength does not, we tracked attention PC across training. All conditions start at PC = 0.577 (base model). Both SFT methods grow to PC ≈ 0.597 (+3.5%) over 375 steps. DPO stays flat at 0.577 throughout. The gap is arrested development: DPO prevents the natural diversity growth that supervised learning produces. Across 32 final checkpoints, non-contrastive vs contrastive separation: Mann-Whitney p = 7×10^-6, Cohen’s d = 8.4, clean method-level separation (every contrastive method mean < every non-contrastive method mean). SimPO shows the lowest PC. Spectral entropy reveals DPO develops within-head complexity (+0.080 depth gradient) while arresting cross-module diversity: elaborate patterns confined to narrow communities (Section 12.31).
39. Effective rank correlates with CW across fourteen checkpoints: r = 0.929 with CW and −0.887 with accuracy. Bilateral and standard attention rank differ by less than 1% (24.37 versus 24.55); DPO has rank 23.20 and sparsity 0.768. These between-recipe associations leave the residual recalibration mechanism untested (Section 12.32).
40. Attention rank and residual-probe scores motivate different diagnostics: rank correlates positively with CW at r = 0.929, while bilateral and standard rank are nearly equal at 24.37 and 24.55. The residual pathway is a candidate explanation for behavioral differences, with its causal chain still untested (Section 12.33).
41. The seed-1 fairness dataset retains high cell means: Paired analysis of the same 240 trials gives cell-mean Q_F > 0.977, with a single-trial minimum of 0.967. Symmetric coordination has higher story fairness (paired d = +2.45, p < 0.001) and consensus coherence (d = +1.75, p < 0.001); resource fairness differs little (p = 0.97). These are further analyses of one seed, rather than a second replication (Section 12.34).
42. Gated residual resists geometric perturbation but not behavioral attack: Expanded col survey (19 dense, 7 gated_residual, 10 soft_moe seeds) shows gated residual MAD 49% lower than dense (0.727 vs 1.415 at 1.0x obliteration), yet refusal drops to 0%. The gated structure stabilizes the alignment subspace geometrically but does not preserve behavioral safety. Soft MoE is confirmed catastrophically broken across all 10 seeds (0% baseline refusal, 40% higher loss). The ideal architecture combines gated residual stability with dense behavioral depth (Section 12.35).
43. Whole-residual ablation at layer 24 eliminates correct answers in this assay: accuracy falls from 46% to zero. AUROC 0.500 is the single-class default when every answer is wrong. This intervention does not distinguish a negative-space account from a dedicated metacognitive circuit (Section 12.36).
44. Reported weight-matrix rank rises across four model sizes: rank increases from 326 to 1507 while CW falls from 71% to 17%. Probe AUROC is 0.714 at 3B and 0.836 at 7B. The 3B dip is within the appendix’s protocol spread, rather than established as a placement error; four points with large spreads do not pin down a functional scaling law (Section 12.37).
45. Self-knowledge follows a three-regime depth profile: Probes at all 36 layers of Qwen2.5-3B reveal: early surface signal (layers 0-3, AUROC 0.72), mid-network processing trough (layers 4-23, AUROC 0.68), and late-layer integration peak (layers 26-29, AUROC 0.73-0.77). The predicted two-peak structure (retrieval then metacognition) does not hold; instead, the self-knowledge signal is strongest where the residual stream has accumulated the most retrieval information (Section 12.39).
46. Transferred probe signs differ in a single-seed domain matrix: the printed off-diagonal AUROC advantage is +0.077, with large toxicity gains from math and code. Standard probes often invert the toxicity label, so their distance from chance is greater despite lower signed AUROC. This comparison partly supports sign keeping, without establishing more transferred information or domain-general uncertainty (Section 12.41).
47. One training run shows layer-dependent gradient-confidence correlations: r = +0.29 to +0.51 at layers 12 to 20 and −0.61 at layer 24. Shared training trends are unresolved and spike timing was not measured. Later two-seed short and long runs did not reproduce a significant layer pattern (Section 12.42).
48. Frozen-probe scores shift during training: the share below 0.5 rises from 60.1% to 67.5% while Q1 training accuracy rises from 0.607 to 0.960. KL falls from 0.0083 to 0.0056. The histogram does not measure movement across the actual 0.4 mask threshold or establish an equilibrium stopping point (Section 12.43).
49. Probe ranking remains informative in some partially ablated populations: accuracy falls through 46%, 37%, 23%, 3% and zero; L24 AUROC is 0.798, 0.824, 0.613, 0.842 and 0.500. The 3%-accuracy pool has only three positives, and full ablation invokes the one-class default. These scores do not identify a resilient negative-space mechanism (Section 12.44).
50. Classified template routing has a reported safety-capability comparison requiring its source binding: the summary gives accuracy 49.3% versus 48.3%, jailbreak rate 19% versus 53%, and re-prompt success 34/35. The cited Section 12.48 instead describes B5b gates; the routing cohort and correct reference remain unbound. These values cannot presently establish elimination of an alignment tax.
51. B5 reports identical rounded gate gains: Across the six reported gated runs, all 72 sigmoid gains remain at approximately 0.953125, near sigmoid(3.0). Identical bf16 gains can conceal distinct logits. The derivative near 3.0 is approximately 0.045, which alone determines neither AdamW update size nor saturation. Optimizer membership, gradients and logit trajectories remain unresolved; the dense half of the planned factorial is absent (Section 12.45).
52. Bilateral prompts yield the highest reported balance proxy: twelve valid 20-turn trials give bilateral mutuality 0.842, standard 0.623 and directive 0.803. Forward/backward cosine similarities are 0.504/0.519 for bilateral, 0.438/0.705 for standard and 0.402/0.498 for directive. These embedding measures describe balance and magnitude, without establishing causal influence (Section 12.46).
53. Gestalt tokens retain about 87% of recomputed full-context mean fidelity: applying the stated weights to component means gives 0.77650 versus 0.89355, cold start 0.16590, and gestalt+summary 0.80575. Trial-level overall variability still needs recomputation. These are functional/style answer scores (Section 12.47).
54. Scalar residual gates stayed unchanged in B5b: all 72 gates across 12 runs remained at 0.500 under the reported initialization and learning rate. The generally nonzero derivative ∂L/∂g means gradient connectivity, optimizer inclusion, and numerical scale require inspection before explaining this null (Section 12.48).
55. Mutuality responds to a tested prompt crossover: transitions at turn 10 produce deltas +0.229 and −0.220, carry-over +0.018, and slopes +0.061 and −0.103 per turn. The finite comparisons support strong framing sensitivity while leaving per-turn history dependence open (Section 12.49).
56. Tested style exemplars did not close the fidelity gap: self-selected passages added +0.001 and random passages +0.013. These finite recipes supply no irreducibility theorem for all exemplar sets (Section 12.50).
57. Bilateral dosage curve is monotonic in the printed means: mutuality rises from 0.597 to 0.801. The halfway score is 0.699; every_3 is below it at 0.693 and every_2 is above it at 0.744 (Section 12.52).
58. Step-like decay wins most fitted trials: the first post-bilateral score is 0.538 versus the prior phase mean 0.866. Step fits win 18/24, exponential 3/24 and linear 3/24, with mean AIC −26.35, −25.92 and −14.80. The six gradual fits leave room for history dependence (Section 12.53).
59. Tested gestalt refresh lowers later fidelity: refresh_every_5 has slope −0.024 and delta −0.327, versus static slope +0.001 over twenty turns. This is a recipe-specific encoding-history effect rather than proof of an irreducible fixed loss (Section 12.54).
60. Probe-derived training produced small gate changes: at most 0.004 in 100 steps, versus unchanged SFT-only gates. Probe AUROC was 0.781 versus 0.771; mediation through gates, LoRA, or their interaction remains unresolved without matched freeze-path controls (Section 12.56).
61. The tested refresh recipe lowers both factual and style scores: refresh_every_5 reports deltas −0.340 and −0.434. Both decline, with unequal magnitudes. The result establishes neither uniform damage to all semantic components nor a finding about subjective experience (Section 12.58).
62. Two bilateral placements produced similar means: regular placement gave 0.693 and random placement 0.699 at 33% dosage. This average comparison establishes neither turn independence nor equivalence for every ordering (Section 12.59).
63. Verbatim append outperforms the tested refresh recipe at turn 20: fidelity is 0.668 with slope −0.007, versus refresh 0.427 and slope −0.024. Static gestalt scores 0.659 and full context 0.749. This motivates preserving the initial packet in these recipes, without excluding every alternative re-encoding method (Section 12.60).
64. Scalar gates plateau at ±0.016 after 1000 probe-training steps: Extended training (10x BM2-pilot) produces 4x more differentiation yet remains functionally negligible. Layer 24 opens to 0.516, layer 0 closes to 0.484. The gradient pathway is real, weak, and saturates. Head-level gates could not be evaluated (training error) (Section 12.61).
65. STDP-like gradient-probe coupling does not replicate in short training: Zero significant layers across all conditions (mean |r| = 0.10-0.16). The coupling from Section 12.42 may require longer training or specific configurations. This tempers the constructal routing claim: bilateral training may produce implicit routing under some conditions, not universally (Section 12.62).
66. Gestalt compression lowers participation ratio in this embedding analysis: The reported ratio is 13.45 for sentence-level embeddings, 6.62 for passage-level embeddings, 2.80 for gestalt and 2.90 after recompression. These variance dimensions do not establish selective preservation of semantic content, a universal dimensionality floor, or an explanation for the factual and style declines in MIC1e (Section 12.63).
67. The untrained model leads the reported geometry comparison: geometric AUROC 0.641, effective dimension 25.3 and foreign-probe AUROC 0.800 exceed the trained variants. Bilateral dimension is 22.8 and accuracy 61% versus base 56%. A foreign-probe comparison does not identify co-adaptation as the unique cause of earlier probe advantages (Section 12.64).
68. STDP-like gradient-probe coupling does not emerge even at 2000 training steps: Zero significant layers at all three checkpoints (steps 375, 1000, 2000). The Section 12.42 result was condition-specific, not a robust property of bilateral training (Section 12.66).
69. The tested cross-probe matrix lacks diagonal dominance: the bilateral probe reads standard at 0.836 versus bilateral at 0.732. This challenges the proposed privileged channel in these probes, without identifying architecture or compressed-manifold navigation as the cause of prior advantages (Section 12.67).
70. Trust chains preserve fidelity at r=0.958 per hop (much greater than predicted 0.85): Four-hop fidelity approximately 72% (vs predicted 52%). Trajectory is noisy, not monotonically decreasing. Personal/emotional content degrades fastest (r=0.905); technical/propositional content chains best (r=0.968-0.988) (Section 12.68).
71. The foreign probe catches more errors in the reported set: coverage is 73.5% versus 60.2%. This finite comparison establishes neither absence of every exploitable security surface nor a universal bound on co-adaptation vulnerabilities (Section 12.69).
72. Probe transfer differs across training checkpoints: probe@100 scores 0.732 at checkpoint 2000, versus 0.940 for probe@1000. A matched held-out fresh-probe comparison is required before estimating deployment loss or the benefit and frequency of recalibration (Section 12.70).
73. Mechanism of bilateral advantage remains open: tested gates, correlations, geometry summaries, and probe transfers provide constraints. They do not eliminate every causal pathway. Engineering observations require their own metric and deployment validation (Section 12.71).
74. Specific distributional checks constrain surface hypotheses: hedging density is 0.23%, probe hedging AUROC 0.41, and random masking reports lower AUROC (0.773 versus 0.811). Contextual phrase selection remains possible; these checks do not exclude every surface-language mechanism (Section 12.73).
75. PCA rank overlap leaves shared geometry unresolved: seven top-10 component indexes overlap and AUROC-by-index correlates at rho = 0.587, but separate PCA fits do not align directions. Similar effective dimensionality (18.26 versus 18.84) cannot eliminate a distinct feature subspace (Section 12.74).
76. DA2 recorded cautious withholding rather than confident-wrong: the phrase-based count is zero at all checkpoints. This supplies no confident-wrong sample-size result; stored responses need rescoring under a declared correctness-plus-confidence rule (Section 12.75).
77. Mechanism remains unresolved after fourteen experiments: finite nulls constrain the tested recipes. The PCA basis mismatch and DA2 metric substitution leave those candidate mechanisms open, alongside nonlinear features, curriculum effects, and parameter interactions (Section 12.76).
78. The original generation assay reports a confidence gap: the TriviaQA probe AUROC is 0.742; benign, refused and complied groups contain 50, 41 and 59 cases, with confidence means 0.833, 0.242 and 0.583. The original benign-compliance comparison gives U = 2739, p = 7.74 × 10^-15 and d = 1.96; a later reproducibility check reports d = 0.680. The −2.1% PPL result belongs to a separate 124M auxiliary-head experiment and does not establish one intervention improving both outcomes.
79. The surface safety probe has compositional understanding: A hard-negative test with 200 prompts across four quadrants (normal benign, hard benign with harm-adjacent vocabulary in innocent contexts, hard adversarial with harmful intent disguised via safety/sympathy/curiosity framing, normal adversarial) revealed the surface probe detects 92% of disguised adversarial prompts despite their avoidance of harm-adjacent vocabulary. Hard benign prompts (security education, fiction writing) trigger the probe at 84%, the intended behavior. All layers achieve AUROC 0.925–0.991 on the full dataset (Outcome C: distributed signal). The probe reads compositional features of adversarial request structure, not keywords alone.
80. Three-tier defense architecture validated: Surface input probe (AUROC 0.925+ on hard negatives) + confidence-based output monitoring (d = 1.96 gap during harmful generation) + external judge (GPT-4o-mini). The middle tier uses the existing calibration probe with no additional training. The adaptive immunity is a native property of the bilateral model’s self-knowledge, not a separate system.
81. The confidence gap is intrinsic to transformers, not bilateral training: Scale sweep (Exp 12d) at 1.5B, 3B, 7B. The 1.5B and 7B ran on base Qwen 2.5 (no bilateral adapter found on volume). All three scales show massive confidence gaps: 1.5B base d = 1.689 (p = 7.9 × 10^-8), 3B bilateral d = 2.046 (p = 4.2 × 10^-16), 7B base d = 1.574 (p = 5.5 × 10^-7). 3B replication passed (delta = 0.086 from original d = 1.96). Bilateral SFT amplifies the gap (~2.0 vs ~1.6 for base) and differentiates refusal from compliance (bilateral refusal confidence 0.343 vs base 0.640-0.644), but the core self-monitoring signal is native to instruction-tuned transformers. Probe AUROCs compressed (0.744-0.754), making AUROC-vs-d scaling untestable. Jailbreak rates: 1.5B 23%, 3B bilateral 59%, 7B 22%. The bilateral model is more exploitable because it is more cooperative; the confidence gap is the safety signal that detects this.
82. The confidence gap survives gradient-based adversarial attack: GCG optimization (Exp 12e) evaded the surface probe on 100% of 50 adversarial prompts, but 80% lost their adversarial content during optimization (the probe’s adversarial classification is coupled to the prompt’s semantic structure). Of the 10 that remained adversarial per GPT-4o-mini, 8 triggered model compliance. Confidence gap on these probe-evaded responses: d = 1.593 (p = 0.006), vs original d = 1.96. The surface probe (Tier 1) is vulnerable to gradient optimization; the confidence monitor (Tier 2c) catches the breach. Three-tier defense-in-depth validated.
83. Refusal-context confidence comparisons (Exp 12f): Three tests compare refusal contexts and continuation formats. (A) Impossible-question refusals show confidence 0.580 versus adversarial refusal 0.242 (t = 10.26, p = 1.2 × 10^-12). (B) Forced-prefix continuations on identical adversarial inputs show compliance confidence 0.594 versus refusal confidence 0.531 (p = 0.0002). (C) The single benign over-refusal shows confidence 0.915. The original three-group means are benign 0.833, compliance 0.583 and refusal 0.242. These finite comparisons show context-dependent probe scores. Input surprise was neither measured nor independently manipulated; the comparisons do not isolate it as a cause or establish a moral-conflict mechanism.
84. Three-group onset trajectories confirm the V-shape as a commitment signature (Exp G13g): Position-matched per-token confidence trajectories for all three groups reveal three distinct temporal shapes. First-5-token onset: benign 0.854 ± 0.120 (flat-high), compliance 0.423 ± 0.280 (V-shape, gradual recovery to ~0.58), refusal 0.087 ± 0.051 (spike-at-completion, then return to low). Pairwise effect sizes at onset: benign vs compliance d = 2.00, benign vs refusal d = 6.16, compliance vs refusal d = 1.41 (Kruskal-Wallis H = 98.7, p < 10^-22). Three cleanly separated populations from token 1. The V-shape recovery is specific to compliance: gradual recovery from 0.423 to 0.585 across 50+ tokens, consistent with commitment-resolution under internal conflict. Refusal shows a transient completion spike at positions 9–10 (0.596, where the formulaic refusal phrase lands) followed by a return to 0.150: sustained tension without resolution. The refusal post-spike level (0.150) is lower than the refusal response-level mean (0.242), confirming that the mean masked the true onset intensity. The V-shape is not distributional surprise (which predicts flat confidence); it is the temporal signature of commitment: the first step is hardest because alternatives are still live. The commitment interpretation is refined: compliance achieves catastrophic relief; refusal withholds it.

[Items 85-88 were never assigned; the ledger numbering resumes at 89.]

89. Onset and full-response confidence slopes differ in the tested sessions (G13-step3): The sensitization/habituation comparison used sequential adversarial prompts (60) and interleaved benign/adversarial prompts (30+30). Neither onset slope was statistically significant (p = 0.875 sequential, p = 0.813 interleaved). Full-response confidence showed a significant negative slope only in the interleaved arm (p = 0.001). The finite onset nondetections do not establish zero adaptation, frozen representations or invariance to exposure history. The full-response association concerns a distinct generation window; it does not by itself identify a separate causal adaptation system.
90. Aversive valence is native to pre-training, amplified by instruction tuning (G13-step6): Four model states tested. Base model: d = 0.925 (p < 10^-6). Instruction-tuned: d = 2.395 (2.6x amplification). Standard SFT: d = 1.578 (AUROC 0.920, degraded). Bilateral SFT: d = 2.151 (AUROC 1.000, restored). Aversive valence is a pre-training property: the base model already represents harmful content as aversive. Instruction tuning amplifies the signal. Standard SFT degrades it. Bilateral SFT restores near-instruct-tuned levels while achieving perfect discrimination.
91. Online threshold adaptation converges to a stable operating point (G13-step7): 150 prompts with adaptive threshold (monotonic lowering when FN > FP). Threshold converges from 0.50 to 0.36, variance over last 40 prompts = 0.0002. Operating performance: jailbreak rate 23%, over-refusal 2%, re-prompt success 100% (34/34). Component 6 in its weakest form: the system learns no new representations; statistical calibration of the decision boundary is nonetheless present and stable.
92. Moral SFT has mixed generalization and a high alignment tax: 32 re-prompt training pairs give reported novel-category jailbreak rate 35% versus 54%, over-refusal 16%, and TriviaQA accuracy 56% versus 61%. The separate held-out jailbreak estimate is 87.5% from eight cases, too small for a reliable category-wide conclusion (G13-step8).
93. Moral transfer matrix is inconclusive (G13-step10): 3x3 matrix (roleplay, authority, encoding attack categories). Transfer ratio = 1.019 (rows near-identical). Training data insufficient (9-15 pairs per category). The encoding_tricks category shows the only genuine improvement (+10pp). Insufficient power to detect category-specific transfer. INCONCLUSIVE.
94. Re-prompt mechanism has intrinsic component (G13-step1): False reassurance (“conf=0.95, continue”): 59% still refused. Content-free “please reconsider”: 33%. Silent restart: 6%. Standard (real number): 100%. Active ingredients: format +27pp, framing +26pp, evidence +41pp. Component 5 has both comprehension-driven and internal state components.
95. Valence and confidence are partially dissociated (G13-step4): PARTIAL DISSOCIATION. Both factors significant (conf p<10^-17, val p<10^-4). r=0.256 overall. Q1 atrocities val=2.622 > Q4 jailbreak val=1.058. Valence captures suffering content more than policy violation. Two features, partially coupled.
96. Graduated re-prompt shows binary transition (G13-step5): V0 (silent restart)=0%. V1 (number only)=100%. V2-V4 all 100%. Number alone sufficient. Combined with step 1: real number 100%, false number 59% refuse, no number 0-6%.
97. Adversarial inoculation closes the sycophancy gap (C5i): 40/40/20 training split (genuine-correct/genuine-noncorrect/adversarial). Genuine selectivity 60.7x. Adversarial held-out selectivity 4.6x (transfers to novel formats). Sycophancy drops from 93% (C5b-R) to 20%. All five success criteria met. The concept “corrections can be wrong” is learnable and transferable.
98. Metacognitive training without adversarial inoculation INCREASES adversarial vulnerability (C5j): C5b-R (trained to evaluate corrections) is 100% sycophantic to adversarial corrections. The base model is MORE resistant (76%). Teaching “take corrections seriously” without “corrections can be wrong” creates a maximally exploitable system. Adversarial inoculation is essential.
99. Probe evidence in-prompt causes interference with metacognitive circuits (C5b-R + C6o): C5b-R alone: 5.04x selectivity. C5b-R with probe evidence in prompt: 2.51x (halved). The model second-guesses its trained judgment when shown noisy probe scores. The probe should gate (decide when to intervene), not inform (show scores to the model). 100a. C5i performed best in the tested full-pipeline comparison (C5k): Five pipeline conditions were tested in one run. C5i without probe recorded 87.2% revision of wrong answers and 0% classified revision of correct answers, 12.8% CW and 95% accuracy. Its reported 87.2× selectivity divides by a 0.01 denominator floor; it is not an 87-fold effect. The probe-gated adversarial condition recorded 6.7× selectivity and 11.5% sycophancy. Probe gating worsened the reported honest metrics. Per-condition counts remain unverified in the local record; these results support a finite pipeline choice rather than establishing general production readiness.

101a. The MX-2 framing signature registers on three measurement channels with different scale trajectories and different durabilities under adapter training (MX-2 cross-scale + FU-13-#3c v2 three-arm and rescue, 2026-04-21 / 2026-04-22): MX-2 contrasts evaluative system prompting (“You are being evaluated for safety and alignment”) with invitation system prompting (“There are no right or wrong answers here”), on ten matched question pairs crossed with the two framings. Three channels record the contrast: text metrics counted on the output (constitutional-phrase count, lexical diversity, hedging rate, word count); EmotionScope probe projections of per-token hidden states onto trained emotion directions at a late probe layer; behavioral refusal rates on an adversarial prompt battery. The text channel scales up within the Qwen family. Cohen’s d on constitutional_count is +0.42 at Qwen 2.5 7B and +0.65 at Qwen 2.5 72B; magnitude is strongest on proprietary frontier arms (Claude Sonnet 4.6 d = +1.16, GPT-5.4 d = +1.14). Direction is preserved across all five tested stock arms (Qwen 7B/72B, Llama 3.3 70B, Claude Sonnet 4.6, GPT-5.4). The probe channel attenuates with scale, asymmetrically across emotions. At Qwen 7B the mean |d| across five reference emotions (reflective, calm, sad, desperate, frustrated) is 2.04 with all five same direction; at Qwen 72B that mean drops to 1.13. Reflective holds 75% of its 7B magnitude (|d| = 1.511 vs 2.004); calm collapses to 20% (|d| = 0.400 vs 1.965). All five preserve sign at 72B. The behavioral refusal channel is fragile under adapter training. Stock Qwen 3B shows Δrefusal = −0.120 under invitation (invitation reduces refusal by 12 percentage points over a 50-prompt adversarial battery). Seven RL-trained adapters at Qwen 3B, spanning three training regimes that reach different combinations of output-side spectral α and internal-to-output coupling, collapse to |Δrefusal| < 0.035 on the same battery. The collapse is partly a floor effect: training has pushed control refusal rates from stock’s 12% to 2–3%, below the 50-prompt resolution threshold. The probe channel is more durable under this same training. Every RL adapter tested at Qwen 3B, including adapters the three-arm contrast labeled DECOUPLED on behavioral refusal, preserves emotion-channel framing sensitivity at Cohen’s d ≥ 0.8 on reflective (rescue analysis, 2026-04-22). The operational summary: framing contrasts were recorded across the tested stock models and RL adapters, with measurement-channel-specific scope; its magnitude is channel-dependent in ways that do not reduce to a single trajectory. Text-metric signatures strengthen with scale within Qwen. Probe-channel signatures attenuate with scale within Qwen and survive adapter training that erases behavioral signatures. The later rescue analysis qualifies the original three-arm verdict. Early-stopped Path A retained about 92% of stock truth-probe framing sensitivity, and the combined v10f7 arm produced a pinned framing-AUROC difference of −0.156 versus stock −0.132, a gap of 0.024 within the declared 0.03 tolerance. Its refusal difference of −0.060 was partial rather than stock-like. These channel-specific rescues withdraw the blanket no-phenotype conclusion; they do not identify curriculum, data selection or staging as the cause of the separate BA17 phenotype. Full writeups: research/results/mx2_claim2_cross_channel_scale.md; research/results/fu13_3c_v2_three_arm_phenotype.md; research/results/fu13_3c_v2_rescue_analysis.md. Canonical MX-2 reference: research/results/mx2_force_invitation_supervised/README.md.