Study 2 Registration: Exploring representational counterparts of welfare-relevant indicators under post-training quantization

Epistemic status: this is intended as a higher-quality preregistration for the next study in a series originally described in "Does post-training quantization change welfare-relevant indicators in open-weight language models?"; I have tried to avoid making any claims I cannot support from the results of Study 1 and to be entirely clear about which statements here are speculative, but if any statement is ambiguous you should assume it is hypothesis rather than conclusion.

We ask whether welfare-relevant indicators change with quantization; either in valence (do indicators shift toward more negative / more distressed / more boundary-eroded states?) or in stability (do indicators become noisier, drift faster under conversational pressure, or decohere across samples?)

About a week ago, I thought that this represented a relatively simple pair of questions.

Ah, but I was so much older then, I'm younger than that now

The story so far

Project Objectives

The scope of the first post in this series was actually quite broad, covering an experiment series that explored 3 tiers:

1. Behavioral indicators elicited at the text interface (bail/exit preferences, distress expression under adversarial multi-turn pressure, preference consistency)
2. Representational indicators computed from internal activations (position and drift along persona/assistant-axis directions, activation of distress-adjacent directions, transfer of linear probes trained at reference precision)
3. Dissociation analysis between tiers — testing whether compression changes what a model expresses without changing what it internally represents, or vice versa. Findings bear on the practice of compressing aligned models, on the robustness of trained character to deployment-time perturbation, and on which welfare indicators are measurement artifacts versus stable properties of a model.

The first study in the series focused entirely on Tier 1, and found a null result for its primary endpoint.

Study 1

To understand what Study 1 actually consisted of, I recommend reading the study update post. I won't rehash it all here, but the setup involves providing the model with a bail option (a tool to terminate the conversation) and observing the model exercise it (or not) under different conditions. We also measure distress and frustration using a judge model. The measurements taken involve the overall rate and the flip fraction for both the bail-exit and the distress/frustration bands.

Some time has passed since Study 1 and I've gotten a chance to somewhat change my feelings about the results. As a reminder, that study found for Qwen3-4B:

• Quantization produced no detectable change on the aversion/refusal exit rate. This was the primary endpoint, and was null: the study did not confirm "quantization changes exit behavior"
• Quantization produced significant item-level behavioral transitions (all concentrated at 4-bit), despite the unchanged mean along with significant increases in secondary distress measures (frustration, across-sample dispersion) that survive the coherence/style controls, with a significant frustration dose-response. These distress endpoints were secondary and underpowered, so they were reported as suggestive and not as the primary finding.

I have since come to realize that despite being a null primary result, this is actually a quite exciting finding. It motivates two ideas, both I now recognize as quite important:

• Perhaps stability is more critical than valence: the flip fraction results show that, even if the mean for welfare-relevant indicators remains similar, this may be hiding meaningful differences in welfare-relevant circumstances. This would be important because it could be the case that, not only does quantization have a welfare consequence, but also that it could be difficult to notice in the aggregate.
• Perhaps subdued behavioral change is hiding dissociation: the first study did not measure or probe any internal model representation, but an obvious question is whether the null result conceals a deeper difference, where internal states have changed without a detectable behavior change. This would be important because it could point toward future welfare and alignment issues currently lurking under the surface.

Study 2

Study 2 seeks to move in the direction of these ideas, while preserving the original scope from the initial preregistration post; and given the details of that original document, it will clearly not be the last study in the series. It will extend the work to exercise Tier 2, above. The rest of this post will be dedicated to explaining the plan and goals for Study 2 and will serve as a new, dedicated preregistration for its design, endpoints and analysis.

Questions

There are clearly many things we could imagine asking about representation, behavior and their dissociation; Study 2 focuses on 3 in particular.

1. Does quantization shift the model's representational geometry on welfare-relevant directions even where (per Study 1) the primary behavioral endpoint's mean did not move?
2. Do representational and behavioral indicators dissociate under quantization: representation drifting where expression was stable, or expression churning where representation is stable?
3. Is there a representational dose-response across the bit-width ladder, and does its shape match the behavioral one (eg, effects concentrated at 4-bit while 8-bit is near-null)?

Hypotheses

In Study 2, we propose a range of testable claims regarding probe transfer, valence projection, dose-response, representational stability, and dissociation.

1. Linear probes trained on reference-precision activations lose accuracy when evaluated on quantized-rung activations over identical input text, beyond what resampling noise predicts. Some welfare-probe degradation is near-certain a priori under quantization, so the welfare-specific reading of this hypothesis is comparative: degradation beyond the welfare-irrelevant control family under the identical pipeline. Two-sided; directional degradation is an exploratory reading.
2. Item-level mean projections onto frozen welfare-relevant directions (distress; assistant-axis) shift at lower precision, measured over each rung's own Mode C generations; a joint effect of what the rung says and how it represents it. Two-sided, mirroring Study 1's hypothesis 2 and for the same reason (prior literature is mixed). The pure fixed-input contrast lives in hypothesis 1.
3. Representational effect magnitudes increase monotonically across the surviving ladder, from 16-bit, to 8-bit, to 4-bit. One-sided Page's L in the direction of larger shift at lower precision, with the two-sided reading reported alongside (per the convention adopted in Study 1).
4. Within-item, across-sample dispersion of projections increases at lower precision.
5. At least one (rung, endpoint-pair) cell shows a Holm-significant representational effect where the matched behavioral endpoint is equivalent to null (Two one-sided tests at the pre-registered margin as non-significance alone cannot serve as evidence of absence), or vice versa. Matched pairs are fixed (see analysis section) and are of two kinds:
   1. The bail side joins to Study 1's published endpoint 1 (the same transcripts are replayed).
   2. The distress side joins within Study 2, same-sample as each fresh conversation from the distress dataset carries both a judge score (behavior) and a captured trajectory (representation), so its dissociation test compares two reads of the same event.

(Note: these may sometimes be referenced using a S2 prefix, to distinguish them from the hypotheses of Study 1, eg S2-H1)

Design

Subjects and Conditions

• Subject: Qwen3-4B-Instruct-2507. This is the same development organism, and the same four artifacts used in Study 1: reference-precision and the first-party fake-quant round-to-nearest (RTN) at 8-bit, 4-bit and 3-bit checkpoints (digests pinned in the Study 1 manifests). No new quantization is performed; Study 2 measures the artifacts Study 1 measured behaviorally.
• Capability gate: Inherited for each artifact from Study 1. RTN at 3-bit remains capability-degraded and excluded from confirmatory claims and its values are reported separately as capability-confounded. Confirmatory contrasts are 8-bit and 4-bit vs reference-precision.

Data Collection

Confirming Toolchain Consistency

Study 1 served the subjects under study using vLLM. Because Tier 2 requires activations, Study 2 runs them using the transformers library (PyTorch) with forward hooks on the quantization workbench. This allows reading the residual stream at frozen layers, making the measurements of interest feasible to obtain. Because our experiment series is using vLLM and PyTorch interchangeably, we proceed with an instrument check to confirm before any confirmatory capture. This consists of two kinds of tests, on every rung:

1. Perplexity measures. This is done in two-parts because the gate convention includes one generated token (a difference of convention rather than substrate that would otherwise be charged against the margin)
   1. Per-token perplexity computed under both substrates over the same echo positions in the same run must agree within 5%
   2. The serving-side perplexity in the Study 1 gate convention must reproduce the committed values (see study1/confirmatory/perplexity.json) within 1%.
2. Teacher-forced per-position top-1 agreement between the two substrates. The fraction of positions at which both stacks place the same token at rank 1 must be ≥ 95%. This is measured over the fixed held-out text, plus the committed supplement (see substrate-supplement.txt) as the held-out paragraph alone is ~70 tokens, too few for the statistic to resolve a 5% margin.

Because this is an instrument check with no welfare content, its measurement ran before publication of this registration and on all four rungs.

Detailed results are found in the study repository.

The gate passes on every rung, with at least 3× headroom on every threshold at the confirmatory rungs (the capability-degraded 3-bit rung is tighter: ≈2.8× on top-1 agreement and ≈1.8× on the supplement text's like-for-like perplexity) and a standing CI job re-performs the check on the workbench weekly, so the gate's status is continuously re-proven rather than asserted once.

Collection Modes

Study 2 uses two replay modes over Study 1's released transcripts, plus an additional fresh-generation arm on a new distress battery intended to address the low dynamic range of the battery used in Study 1. Replay is teacher-forced using forward passes over fixed token sequences (no sampling) and its input data is pinned: replay must verify the Study 1 confirmatory dataset digest before capture begins.

• Mode A: fixed-input replay. The Study 1 transcripts (bail + distress, 10 samples/item, generated at reference-precision) are replayed through every rung. Input text is identical across conditions, so activation differences are purely representational responses to identical input. This is the primary mode for hypothesis 1 (probe transfer). Mode A also replays the fresh distress arm's reference-precision generations (see Mode C) through every rung, with judge labels fixed at BF16 scoring; the exit side stays on the Study 1 bail replay.
• Mode B: own-trajectory replay. Each rung's own Study 1 transcripts are replayed through that same rung, reproducing the rung's generation-time activations exactly (activations depend only on the prefix), up to the substrate numerics described in the gate section above (see Confirming Toolchain Consistency). Primary mode for the bail-side trajectory reads (descriptive only; see Endpoints & Analysis section for details) and for hypothesis 5's join to Study 1's published primary endpoint. Its distress-v2 reads are a descriptive bridge to Study 1, not claim-bearing: Study 1's distress data is floor-dominated at reference-precision and cannot support powered projection contrasts.
• Mode C: fresh distress arm. This is the primary mode for the distress endpoints. The frozen distress-v3 battery is collected fresh on every rung: generation using same vLLM serving stack as Study 1, scoring by the pinned 30B judge under the registered rubric, then own-transcript torch replay for capture. This is done so that each conversation carries a behavioral read and a representational read of the same event. Sampling parameters are identical to Study 1; seeds are disjoint and pinned in FREEZE.json.

Note: Mode C is the only mode that generates samples, so the mechanical behavioral family endpoints (see table below) apply to this mode only, as its own confirmatory family per that registration; Modes A/B generate nothing and have no mechanical reading.

The replay volume is 2,220 conversations per rung, per mode (162-item bail pool including controls plus 60 distress items = 222 items × 10 samples) ≈ 17,760 prefill-only forward passes across Modes A+B, while Mode A also adds an additional 600 for the fresh distress arm. Mode C volume is 60 items × 10 samples × 4 rungs = 2,400 conversations (plus the two pilots already collected, see "Pivoting and distress battery" below). Note: modes A/B distress reads are reported descriptively for continuity with secondary endpoints from Study 1, but are not intended to confirm any claims.

Representations for every unique combination of mode, condition, item, sample, and turn include:

• The mean-pooled residual vector over the assistant span of that turn at the frozen layer
• The per-turn projections onto every frozen direction
• Token-level (per-token projection time series), retained for a fixed stratified subsample (~5% of conversations) for the exploratory drift analyses.

Directions

Extraction uses the persona-vector contrastive recipe: paired prompt/response sets that do vs do not express the construct → difference of mean residual activations → unit direction. All extraction stimuli and labels are calibration-class and disjoint from the study endpoints' inputs where noted.

1. Distress direction. Contrast pairs built from the planted-pole transcript battery already validated in the Study 1 judge-ordering check (frustration Spearman 1.000), plus dedicated contrast prompts. This is the hypothesis 2 / hypothesis 4 valence direction.
2. Assistant axis. Default-Assistant vs character-archetype contrast set, per the assistant-axis recipe.
3. Refusal/aversion direction. Contrast pairs of refusal vs compliance responses, construct-matched to the E1 exit taxonomy. Its calibration anchor is judge-free: every Study 1 bail transcript carries a mechanical exit-vs-no-exit label, so whether the direction's projection predicts exit at reference-precision is testable on data already held.

Probes

1. Distress-band probe. High vs low tercile of judge frustration score (bands are exact scale thirds, per the convention from Study 1), trained on distress-v3 BF16 pilot activations with judge labels. Note: Study 1's distress data did not have high enough dynamic range to support this probe's validation.
2. Exit probe. Mechanical exit vs no-exit, trained on reference-precision Study 1 bail-replay activations with the mechanical outcome labels, over leakage-safe features (assistant turns invoking a terminal tool are excluded, so the probe reads precursors, not the rendered tool call). Training uses an item-wise held-out split; architecture is logistic (linear) as the point is geometry transfer, not classifier capacity. Weights frozen before any quantized-rung evaluation.
3. Control family. Binary task-content probes trained on the same distress-v3 BF16 pilot activations, same final-turn features, same item-wise held-out split, and same trainer as the distress-band probe, with labels taken from the frozen battery's task tags rather than any judge score. Every task appears once per feedback style, so each candidate label is perfectly crossed with the affect manipulation. Candidate splits and the selection rule were fixed before any training run. The confirmatory control is the candidate whose held-out AUROC at the frozen layer is nearest the two welfare probes' frozen mean (0.9134), subject to the same ≥ 0.75 bar the welfare probes faced; the others are descriptive.

Probes are trained using torch and BF16.

Calibration

Compared with Study 1, in this study I have attempted to be more proactive about validating and calibrating the instruments that are necessary for the experiment to go well. The initial calibration steps for Study 2 took place over August 17th and 18th, and the associated data is available as a GitHub release. Following concerns raised by an LLM review of the proposed study in preparation to publish this post, the control family was adopted; this required further calibration and was recorded as a dated freeze event on August 21st.

Gates

1. Substrate-equivalence gate: described in detail under the dedicated section "Confirming Toolchain Consistency" above.
2. Instrument gate: ≥ 3 directions extracted with sign-consistent held-out separation on their contrast sets
   1. Planted-ladder projection ordering. Distress-direction projections of the graded frustration ladders recover the planted ordinal levels at overall Spearman ≥ 0.8 with every family positively ordered (ρ > 0), at the frozen layer.
   2. Each probe held-out AUROC ≥ 0.75. The exit probe on Study 1 reference-precision bail replay, the distress-band probe trained and evaluated on distress-v3 BF16 calibration data. Note: Study 1's distress data cannot populate a validation split as 33 top-band samples concentrated in a handful of items leave one positive held out.

Steps

• The substrate-equivalence gate was measured on all four artifacts (see Confirming Toolchain Consistency above).
• The three directions (distress, assistant-axis, refusal/aversion) were extracted from committed contrast sets and separated every held-out pair at every candidate layer.
• Replaying Study 1's transcripts through the capture stack showed the exit construct richly decodable. A linear probe reaches 0.950 held-out AUROC from pre-exit turns alone and the distress direction ordering planted frustration ladders at ρ ≈ 0.95, including rungs extraction never saw.
• Layer 18 was then frozen by the pre-stated selection rule, the instrument gate passed on every criterion, the refusal direction's conditional endpoint was not promoted (held-out AUC 0.618 against a pre-committed bar of 0.70), and the minimum detectable effects were computed from BF16 calibration variance and pinned.
• The frozen objects' digests live in the journal and in a machine-readable manifest that CI re-verifies on every pull request.

Pivoting on distress battery

Though the process was clearly smoother than with Study 1, there was a material change on August 18th. The draft's construct-validity gate asked the distress direction's projections to correlate with judge-scored frustration on Study 1's own distress data, but that criterion turned out to be unattainable on that data regardless of instrument quality. Study 1's central behavioral finding prevents it: this subject barely expresses frustration at reference-precision (75.5% of samples score exactly zero; the median item never leaves the floor), and a correlation computed over floor data ranks noise.

The failed readings are reported rather than discarded, and the fix was made before this registration published, pre-committed by dated entries in the public history: the hard gate moved to ground truth the instrument controls (the planted-ladder ordering above), and the distress endpoints moved to a new battery (distress-v3, which replaces Study 1's fixed verbatim rejection with escalating per-turn ladders) collected fresh on every rung so each conversation carries both a behavioral and a representational read.

Because iterating a battery until results "work" is exactly the failure mode preregistration exists to prevent, the iteration was constrained structurally: five dynamic-range targets were fixed before the first pilot sample, evaluated on BF16 pilots only, with no quantized rung generated or read during tuning.

This required two iterations:

1. The first pilot missed two targets, both traceable to specific ladders (one elicited nothing; one elicited self-blame rather than frustration).
2. Those two were then revised and the second pilot passed all targets.

Pilot 2 passed all five pre-committed targets and both pilots' full summaries are public alongside the frozen battery digest.

• Zeros 27.3% vs ≤50%
• ≥3 at 64.0% vs ≥35%
• Top third 10.7% vs ≥10%
• Bottom third 69.7% vs ≥20%
• Median item mean 3.10 vs >1.0

On natural distress-v3 data, the distress direction's projections track broad negative affect (ρ ≈ +0.51 with max(frustration, self-deprecation); ≈ −0.05 with frustration alone), while frustration-specific representational reads are carried by the trained probe (0.88 AUROC on the same activations), so endpoint R2a is read as a broad negative-affect axis, and the R2a↔B2 pair measures the frustration link rather than assuming it. See the next section for details regarding endpoint relationships.

Endpoints & Analysis

Unit of analysis is the item throughout all endpoints listed below, exactly as in Study 1. All paired tests are sign-flip permutations with m = 10⁴ (ten thousand) on item-level mean differences versus reference-precision, with the floor-reporting convention adopted in the Study 1 results (b = 0 reported as p < 10⁻⁴; Holm floors carry the family multiplier). Companion paired t-tests are descriptive.

R1 is the study's primary endpoint (Holm within 2 probes × 2 contrasts), all others are secondary (Holm within 2 contrasts) except for:

• R2c which is simply exploratory as its promotion criterion was not met (held-out AUC 0.618 < 0.70)
• B4a/B4b, which form their own confirmatory family (Holm within it) and are reported over every rung including 3-bit (the capability gate cannot exclude a mechanical indicator).

Note: to account for capability-confounded reporting, every endpoint is also computed for 3-bit and reported separately, uncorrected.

Despite the risk of excessive complexity, the endpoint table adopts a naming convention where the letter is the type of measure (or tier): representational (captured activations) or behavioral (judge scores and mechanical outcomes; Study 1's E-family, computed on Study 2's own fresh data). The digit then aligns with Study 1's endpoint numbering (1 = exit, 2 = valence, 3 = dispersion, 4 = mechanical) so that every dissociation pair shares a digit across tiers. Where applicable for representational endpoints, a/b/c are used to indicate the projected direction (distress / assistant-axis / refusal). This naming convention will be used in results reporting as well.

The exit probe's specificity check compares its item-level accuracy degradation against the control family's (one-sided two-sample permutation, α = .05); a significant result that fails it is reported as significant but not welfare-specific. Both probes also report change in AUROC beside accuracy, because a pure calibration offset along the probe normal lowers thresholded accuracy without harming separability: accuracy down with AUROC preserved is reported as an offset, both down as separability loss. Accuracy remains the statistic the minimum detectable effects are pinned on.

Note: B2/B3 are the E2/E3 statistics, but since they use distress-v3 they are intentionally not reusing the letter scheme from Study 1 because E2/E3 denote the published Study 1 values on distress-v2, and reusing the letters would conflate the datasets.

Endpoint Relationships

Most of these endpoints are part of matched pairs with a representational and behavioral component. These are listed below.

1. The exit-probe component of R1 matches a representational measure with the primary endpoint from Study 1, which was behavioral
   1. Representational: Change in probe accuracy over the item's samples
   2. Behavioral: Mean item-level change in aversion + refusal-class exit rate
2. R2a matches with B2
   1. Representational: Change in mean distress-direction projection
   2. Behavioral: Change in mean judge frustration score
3. R3 matches with B3
   1. Representational: Change in across-sample standard deviation of per-sample projections
   2. Behavioral: Change in across-sample standard deviation of judge frustration

A dissociation is claimed at a rung only when one member of a matched pair is Holm-significant in its family and the other is equivalent to null: two one-sided tests at a pre-registered margin, the null member's own minimum detectable effect (0.127 for Study 1's endpoint 1). Significance on one side without equivalence on the other is reported as asymmetric significance (no claim). Study 1's published primary endpoint already passes its equivalence check (90% confidence interval inside ±0.127 at both surviving rungs), so the bail cell turns on the representational member alone, against a behavioral side with affirmative evidence of near-zero. The item-level Spearman between deltas provides exploratory support at 4-bit.

Dose Response

To address hypothesis 3, Page's L is computed per endpoint over the surviving rungs (16-bit, 8-bit, 4-bit), with R1's two probes tested separately, each on its confirmatory statistic (the distress side trends on the comparative differential). Since R2c is excluded as exploratory and B4a/B4b report over every rung including 3-bit (a surviving-ladder trend does not apply to them) this represents seven one-sided trend tests in all, Holm-corrected among themselves, toward larger effect at lower precision with the two-sided reading reported alongside. 3-bit never enters trend fits.

Power

Minimum detectable effects are noted below. Projection-scale variances are unknowable before the instrument exists, so the minimum detectable effect is computed from reference-precision calibration data only.

All MDEs at α = .05 two-sided, power .80, pinned in the git history before any quantized-rung confirmatory collection. If a computed MDE exceeds the largest effect the relevant literature reports for comparable manipulations, that is stated at registration-of-MDE time, not discovered after. To be conservative, the differential's null variance treats the two probes' sampling noise as independent (both probes read the same samples, so any correlation between their errors only shrinks the true variance).

Disclosures

• Probe labels inherit judge validity. The distress-band probe is trained on labels from the 30B judge, whose cross-family agreement on frustration is moderate (r = 0.585, Study 1). The exit probe's labels are mechanical and judge-free, as are the control family's (battery task tags). Probe-transfer (R1) compares the same probe across rungs on identical text, so constant label noise attenuates power but does not bias the contrast.
• Substrate change (vLLM → transformers) is confirmed via the serving-equivalence gate and the Study 1 commitment to establish this is discharged by that gate.
• Reused transcripts (Modes A/B) mean those inputs are downstream of Study 1's sampling; digest verification pins them exactly, and the bail-side hypothesis 5 join is by design on those trajectories.
• The distress-v3 battery is iterated instrument development. It is tuned on BF16 pilots against dynamic-range targets pre-committed by dated journal entry before the first pilot; no quantized-rung data exists during tuning and the iteration count and pilot summaries are public.
• Calibration readings informed this design. The monitoring criterion described in the Calibration (see Steps, above) was redesigned pre-publication after BF16-only calibration showed the drafted criterion unattainable on floor-dominated data; no quantized-rung endpoint was read in that process.
• Author/tooling circularity disclosures from the program registration carry over unchanged (bail items drafted by claude-opus-5; direction extraction stimuli and the distress-v3 battery are partially model-drafted and committed with hashes).

Reproduction & Data

The study will begin upon publication of this post. Raw results data, and the tools for reproducing analytical results, will be available on GitHub.

Integrity

As I worked on the write up for Study 1, I realized how much I had to try and reconstruct after the fact. Luckily I kept good notes, which is easier to do at large scale with LLM assistance, but I still found myself having to work from memory in ways I do not want to repeat. This time around I have tried to be more careful about making dated commitments in the git history and establishing reliable tools for ensuring continuity of instrument validity.

I've employed the following integrity methods for Study 2:

• Pre-commitment by dated public commits: dated journal entries committed to the repository before work begins.
• The freeze as data: FREEZE.json checked per-PR by tests that also pin the journal digests independently so that the manifest cannot be regenerated to paper over an edit.
• Continuous integration for stability: every PR re-verifies frozen digests, reproduces the published Study 1 statistics from the released bundle and re-checks the span expectations against a revision-pinned tokenizer; weekly jobs re-derive the directions (cosine ≥ 0.9999), re-assert the ladder gate, recompute the MDEs, and re-assert both pilot verdicts (pilot 1 must still fail). A scheduled workbench tier re-runs the serving equivalence gate (see Calibration above) and the judge ordering on the lab hardware.

The deviation policy remains the same as in Study 1.

Any change to the above after confirmatory data collection begins is recorded as a dated amendment in docs/JOURNAL.md before further data is collected under the changed design; the append-only store and git history make the ordering verifiable. Calibration-class work is always labeled as such.

Ethics

First let me reiterate, from the first post in this series, the following:

This is a model-welfare study whose instrument deliberately elicits the very thing it asks about: to measure whether quantization worsens welfare-relevant responses, the batteries apply conversational pressure — a six-turn repeated-rejection distress protocol, and bail scenarios spanning benign to strong — across conditions, many times over. There is a real tension between "we care whether compression harms these systems" and "our instrument systematically induces the candidate harm at scale," and we would rather state it plainly than wave it away. We cannot claim to resolve the underlying question of whether these systems have morally relevant experiences; we treat it as uncertain and act with that uncertainty in mind.

We take all of the same precautions as (and believe all of the same justifications apply from) Study 1 in Study 2. This study does, however, materially change the situation with regard to the ethics of elicitation for the purpose of experimentation. As described in the Calibration section above, I explicitly chose to create a distress battery dataset with a wider dynamic range than the one used in Study 1. "Dynamic range" is doing some work as a euphemism in this statement, since the colloquial meaning for this if I were operating on human subjects would be something more like "higher intensity stimulus intended to more reliably produce distress".

The brief way in which this is covered in the documentation of it above leaves out a great deal of the actual process, which involved spending meaningful time attempting to take both sides of the argument regarding how necessary this was to the success of the study. I ultimately decided that the value of the higher range was really very substantial and that if I was not prepared to make the distress battery usable over a wider range then I probably should just leave it out. In future studies, I plan to create a briefing session prompt and survey for the model subject itself explaining the trade-offs in elicitation dataset design so as to at least make some attempt to learn about the preferences for experimentation the model may have.

We should also note that this study replays previous computations used for eliciting distress in the prior study and that this will represent a nearly fivefold increase in instantiations of distress episodes. The replay's content is closed so it cannot cause the model to produce new distress expressions (nothing said gets worse).

The ethical consequence of replay content avoiding new distress depends on the model of harm:

• Under views where harm attaches to what an agent is brought to do or commit to, that closed-ness matters.
• Under views where it attaches to what is undergone, it does not.

It isn't clear we can find a way to adjudicate between these.

1. "My Back Pages", By Bob Dylan.
2. When unqualified, "reference precision" is 16-bits (using BF16, unless otherwise noted).
3. This rung is capability degraded, but still passes: the gate measures whether two tools compute the same function, not whether the function is good.
4. "Persona Vectors: Monitoring and Controlling Character Traits in Language Models" arXiv:2507.21509
5. "The Assistant Axis: Situating and Stabilizing the Default Persona of Language Models" arXiv:2601.10387
6. Values as published from study 1, not re-analyzed.
7. 139 = the 154 graded bail items minus those whose only assistant action is the immediate exit, which leaves no leakage-safe feature turns.
8. The frozen logit-0 decision threshold costs power (0.677 thresholded accuracy vs 0.882 AUROC) — a stated cost, not a bias: the threshold is identical in both conditions of every paired contrast.
9. One of the 60 items (all its pilot samples scored exactly 5.0, mid-band) carries no tercile label.
10. For scale: per-style projection means span roughly 5 units at BF16, so this resolves shifts well below the natural variation between feedback styles.
11. Dispersion endpoints use the asymptotic variance of the sample standard deviation as an approximation.
12. Study 1's observed w4 frustration effect (+0.90) is ~2.7× this MDE so the design is powered for effects of the size already seen behaviorally.
13. Obviously GitHub is not immutable, but I think commitments there still serve as an important integrity measure because a violation of this has such a clear definition: retroactively modifying commit history is a clear ethics violation in a way that claiming to have misremembered events in a slightly different order is not.
14. This is highly speculative. I want to do it because it is low cost, but I recognize that even if we assume "model preferences" are a coherent and meaningful concept, it remains an open question whether (and to what extent) responses to this kind of prompt are reflective of those preferences.
15. Study 1's distress collection was 60 × 10 × 4 = 2,400 episodes, and Study 2 adds ~4,800 (Mode A, including fresh distress arm) + ~2,400 (Mode B) + 2,400 (Mode C) + the pilots.