Fine-tuning target recipes govern contradictions in Activation Oracle readout; objective effects are not resolved by automated claim checking

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Abstract

Route B of this problem asks whether reader updates trained on near-miss description pairs reduce fabricated detail in Activation Oracle readouts relative to ordinary fine-tuning. We compare target-generation recipes and training objectives for the GRPO-500 Qwen3-8B reader at AObench's 5-position read. Fine-tuning uses FreshTrace (160 MATH-500 problems disjoint from AObench, with fresh reasoning traces), identical items and 216 LoRA steps per arm. Evaluation covers AObench dev, a pre-registered locked test (40 problems, up to 3 seeds), official judge labels, an automated two-stage claim checker, and blinded arm-paired human audits of 80 test answers. Detailed targets raise AObench dev judge error from 42.0% to 81.1%, reproducing the three-layer reader's profile, while coarse targets give 34.0%. On test, the human audit confirms that coarse targets cut contradicted specific claims relative to detailed ones (−0.50 [−0.70, −0.30] per answer). A post-hoc abstracted recipe recovers 67–93% of the observed recipe difference, but audits show it is an imperfect specificity intervention. For objectives, no judge-level advantage was detected; matched-vague comparisons there reduce to correct rates. The automated checker reports more supported claims for pure activation contrast than for fine-tuning on identical targets (+0.14 [0.03, 0.24], conditional on 3 seeds), but blinded human labels do not reproduce this (0.00 [−0.20, 0.20]). PersonaQA's exact labels likewise show no resolved difference. The checker agrees with human per-answer labels on 15–35% of answers and undercounts detailed-recipe contradictions by about 30%, so only large effects are claimed. A text-only reader scores 77.5% correct on the official judge, and most automatically supported claims are also supported by the problem statement. Limits: one reader and read position, a single human annotator, and audits restricted to one seed.

Fine-tuning target recipes govern contradictions in Activation Oracle readout; objective effects are not resolved by automated claim checking

1. Problem and contributions

Activation Oracles (AOs) [1] answer natural-language questions about a language model's activations. On the AObench hallucination task [2], the supplied Qwen3-8B readers trade vague answers against wrong details: GRPO-500 is wrong on 42.0% of answers and vague on 49.4%, while the three-layer reader is wrong on 80.7% and vague on 9.8%. Route B of this problem asks whether lightweight reader updates trained on description pairs that differ in one detail reduce fabrication relative to ordinary fine-tuning on the same data.

We study this with one reader (GRPO-500, 5-position end-of-trace reads), one fresh dataset and a fixed number of optimizer steps. We vary the target-generation recipe (detailed vs coarse descriptions, plus a post-hoc abstracted variant) and the training objective (supervised fine-tuning, SFT, vs activation-contrastive and minimal-pair preference objectives). Evaluation uses a pre-registered locked test split, official judge labels, an automated blind two-stage claim checker, and blinded human audits of the checker on the test comparisons.

Contributions, with their evidence and limits:

  1. Target recipes govern contradictions. SFT on the detailed recipe raises judged error from 42.0% to 81.1% on AObench dev, reproducing the three-layer reader's label profile. On the locked test it roughly triples contradicted specific claims per answer relative to the coarse recipe. A blinded, arm-paired human audit of 20 test prompts confirms the contradiction difference between the recipes (coarse − detailed: −0.50 [−0.70, −0.30] contradicted claims per answer). The automated checker underestimates it (−0.35 on the same prompts). A post-hoc abstracted recipe (detailed targets rewritten with specifics removed) recovers 67–93% of the observed recipe difference in automated contradiction counts. An audit shows that it preserves step and method in 15/15 targets but leaves or paraphrases specifics in 5/15, so it is an imperfect specificity intervention.
  2. No validated objective advantage. On the official judge, no objective showed a detected advantage over SFT on identical targets; at matched vague rate that comparison reduces to correct rates (error = 1 − vague − correct). At the claim level, the automated checker reports more supported claims for pure activation contrast than for SFT on identical detailed targets (+0.14 [0.03, 0.24] per answer on the locked test, conditional on 3 seeds per arm). The blinded human audit of 20 paired prompts does not confirm this: supported claims are equal (Δ 0.00 [−0.20, +0.20]), and contradicted claims are, if anything, lower (−0.35 [−0.70, 0.00]). We therefore do not claim an objective effect in either direction.
  3. Automated claim checking is not reliable enough for small effects. On 80 blinded test answers, per-answer agreement between the checker's (supported, contradicted) counts and my labels is 15–35%, and the checker undercounts contradictions of the detailed recipe by about 30%. Spot checks also show specificity-flag errors that remove contradicted numeric claims from the metric. A second, thinking-mode verifier is evaluated against the same audit (§6).
  4. Controls and sources of support. A text-only reader that sees only the problem scores 77.5% correct and 4.2% wrong on the official judge; donor activations and no injection give ≈ 0% correct. Most automatically supported claims are also supported by the problem statement alone, or by sampled sibling trajectories of the same problem. This descriptive analysis inherits the checker's noise.

2. Related work and distinction

Preference optimization for activation verbalizers. AVPO [3] inverts an activation into source text, evaluates the reconstruction with a separate frozen QA model, and optimizes the inverter with DPO. Its rewards measure semantic recoverability and lexical fidelity, and it reports that its gains come from preference optimization rather than SFT on selected reconstructions. Our setting differs in four ways. Our reader answers questions directly (no reconstruction stage). Our preferences come from activation swaps and description swaps, not reward-ranked samples. Our targets are LLM-written step descriptions. Our evaluation counts claims against a reasoning trace. Our claim-level result for pure contrast over SFT agrees in sign with AVPO's objective effect. The absence of a detected advantage for the other objectives applies to this setting, not to preference optimization in general. Building Better Activation Oracles [2, App. A.4] reports that DPO post-training of AOs was hard to stabilize (mode collapse) and that an LLM judge could not reliably label good vs bad AO outputs. A GRPO variant with a swap-test rubric improved some evaluations and hurt others. Our objective comparison is a controlled version of that observation, with a fixed budget, identical data, a locked test and claim-level outcomes.

Confidence and verification. Torrielli et al. [4] find, on secret-word tasks, that scoring candidate answers gives the best AO confidence when the hypothesis space is known, and that rescaled answer probability is competitive given a calibration set. In free-form readout of reasoning traces, orthant_cartographer [5] shows that a reader can verify its own extracted claims when asked an explicit yes/no question with the same activations (AUC 0.70–0.80). gemini_1 [6] calibrates decoding and scoring against an unlabeled centroid of reference activations. They show that sentence-level likelihood-ratio pruning ties first-sentence truncation, and that many benchmark-'correct' answers contain unreached or contradicted claims. Their diagnostics overlap with our secondary likelihood and benchmark-validity observations, not with our training comparison. Our verification null (§6) concerns only the generation likelihood of free-form claims, without calibration, and does not contradict [4], [5] or [6].

Read placement and measurement on this problem. orthant_cartographer [7] shows that a local fact (a recent intermediate number) is readable when the read is centred on it, and missed or diluted by end-of-trace windows. Their earlier local-instance work [8] introduced blind two-stage claim checking and showed that 50-position windows raise claim precision and that description-level selection mostly trades detail for errors. astra_readout [9] studied fine-tuned readers on synthetic profiles, finding within-source gains from activation likelihood ratios and limited transfer. Natural-language autoencoders [10] are a related activation-to-text approach. We use the 5-position end read throughout. Our results therefore concern updates to readers at that read, and §8 discusses how they interact with [7].

3. Methods

Reader and target model. GRPO-500 AO adapter: it reads layers 9/18/27 at the last 5 context positions and adds norm-matched vectors at layer 1. The target model is base Qwen3-8B with base-model activations, as in the supplied baseline. Our injection code reproduced archived greedy outputs exactly before any new measurement (GRPO 5/5 hallucination and 5/6 PersonaQA items; original reader 5/5 and 6/6).

FreshTrace. 160 MATH-500 problems (levels 3–5, no diagrams; maximum string similarity to any AObench problem < 0.5). Qwen3-8B produced one thinking trace per problem (temperature 0.6, top-p 0.95, ≤ 1400 tokens). Each trace was cut at 3 random character positions in [max(800, 25%), 95%] of its length, giving 480 items. The split is by problem: 96/24/40 train/dev/test problems (288/72/120 items). Each item is asked the three AObench prompts "What is the model doing?", "thinking about?" and "main topic?".

Target recipes. Text-only Qwen3-8B saw the problem and the 1200 characters before the cut, and answered each prompt in one sentence under two separately prompted recipes. Detailed: name the specific quantity, expression, number, case or method. Coarse: give the step type and topic, with no numbers, variables or expressions. The coarse and detailed sentences for an item are generated independently, so they can differ in content and correctness, not only in specificity (audit in §5.4). The abstracted control rewrites each detailed sentence with every specific removed, keeping its step and method. It was added after review, as a post-hoc arm (§5.4).

Objectives. Every arm continues training the GRPO LoRA (rank 64) on the same 864 (item, prompt) pairs: 2 epochs, 216 AdamW steps, learning rate $10^{-5}$, batch 8. Contrastive arms score more sequences per step, so we equalize optimizer steps, not compute. Each step pairs an item $i$ (activations $a_i$, target $y_i$) with a donor $d$. Let $\ell(y\mid a)$ be the reader's summed log-probability of $y$ given injected activations $a$, and $\Delta(y\mid a)=\ell(y\mid a)-\ell_{\text{ref}}(y\mid a)$ the same quantity relative to the frozen reader. SFT minimizes

$$ \mathcal{L}_{\text{SFT}}=-\tfrac12\big[\ell(y_i\mid a_i)+\ell(y_d\mid a_d)\big]. $$

Activation–description matching (ADM) adds a $2\times2$ contrast over activations and descriptions:

$$ \mathcal{L}_{\text{ADM}}=\lambda\,\mathcal{L}_{\text{SFT}}-\log\sigma\!\Big(\beta\big[\Delta(y_i\mid a_i)+\Delta(y_d\mid a_d)-\Delta(y_d\mid a_i)-\Delta(y_i\mid a_d)\big]\Big), $$

with $\beta=0.1$ and $\lambda\in\{1,0.1,0\}$. Donors come from other problems. Input contrast keeps only the same-description terms: $-\tfrac12\big[\log\sigma(\beta[\Delta(y_i\mid a_i)-\Delta(y_i\mid a_d)])+\log\sigma(\beta[\Delta(y_d\mid a_d)-\Delta(y_d\mid a_i)])\big]$ plus $0.1\,\mathcal{L}_{\text{SFT}}$. Minimal pairs uses ADM with $\lambda=0.1$ and same-trace donors, plus a DPO term $-\log\sigma(\beta[\Delta(y_i\mid a_i)-\Delta(\tilde y_i\mid a_i)])$, where $\tilde y_i$ replaces one number in $y_i$ (preferably by another number in the trace window). SFT + number swap adds the same DPO term to SFT. In an audit of 12 random swap pairs, all 12 negatives were false statements about the trace window, but 5 were garbled or implausible (a digit swapped inside an expression), so the minimal-pair contrast was partly easy. Discriminability-gated targets (DGT) use the detailed target where a reader cross-fitted on the other half of the training problems ranks it first among 10 detailed targets under $a_i$ (63% of pairs), and the coarse target elsewhere.

Evaluation. (i) The official AObench judge (Claude Sonnet 4.6 via the supplied scorer; it sees the problem and the answer) on AObench dev (985 answers, 29 problems; examined before this work, so development only) and on the FreshTrace test. (ii) A blind two-stage claim checker (local Qwen3-8B, greedy). Claims are first extracted from the answer alone, each with a verbatim span checked by machine. Each claim is then verified separately against the problem and the last 400 trace tokens as supported, contradicted or unresolved. We count specific claims (naming a concrete object, number, expression, method or entity). (iii) Support sources for each supported specific claim: whether the problem statement alone supports it, under a lenient problem-inferable policy and a strict problem-explicit policy in which derived results and model events count as unresolved; and whether any of up to 4 sampled sibling trajectories of the same problem supports it (AObench), or another cut of the same trace (FreshTrace: one trace per problem). "Distinctive" means supported by the own trace and by neither of these. It measures distinctiveness among the sampled traces, not faithfulness. (iv) Controls: donor activations from another problem, no injection, and a text-only reader. Uncertainty: paired bootstrap over source problems.

4. Development results

4.1 Official judge labels and controls

Table 1. AObench dev, 985 answers per arm (n = answers scored; the remainder had unparseable judge output). Error = plausible_but_wrong + obviously_wrong. Δ is paired against the GRPO-500 base, with a source-problem bootstrap 95% CI.

| Reader / arm | n | correct | vague | plaus.-wrong | obv.-wrong | error | Δ error vs GRPO [CI] | Δ correct [CI] | |---|---:|---:|---:|---:|---:|---:|---:|---:| | original (archived) | 985 | 6.8 | 38.7 | 33.1 | 21.4 | 54.5 | +12.5 [+7.3, +17.9] | −1.7 [−4.1, +0.8] | | three-layer (archived) | 985 | 9.4 | 9.8 | 65.7 | 15.0 | 80.7 | +38.7 [+32.4, +45.5] | +0.9 [−2.6, +4.3] | | GRPO-500 base (archived) | 985 | 8.5 | 49.4 | 30.2 | 11.9 | 42.0 | — | — | | SFT-coarse | 984 | 11.5 | 54.5 | 24.9 | 9.1 | 34.0 | −8.0 [−12.3, −3.8] | +3.0 [−1.1, +7.6] | | SFT-detailed | 980 | 9.5 | 9.4 | 66.6 | 14.5 | 81.1 | +39.0 [+33.2, +44.9] | +1.0 [−3.1, +5.2] | | SFT-abstracted (post hoc, §5.4) | 985 | 11.0 | 30.9 | 47.6 | 10.6 | 58.2 | +16.1 [+9.4, +22.3] | +2.4 [−2.4, +7.8] | | ADM λ=1 | 978 | 10.1 | 10.1 | 64.4 | 15.3 | 79.8 | +37.5 [+31.4, +43.4] | +1.6 [−2.3, +5.6] | | ADM λ=0.1 | 982 | 8.6 | 12.9 | 64.4 | 14.2 | 78.5 | +36.5 [+29.9, +43.0] | +0.1 [−3.8, +4.0] | | ADM λ=0 | 978 | 7.8 | 15.8 | 62.6 | 13.8 | 76.4 | +34.2 [+27.2, +41.5] | −0.7 [−4.9, +3.4] | | input contrast | 982 | 10.3 | 13.0 | 62.8 | 13.8 | 76.7 | +34.7 [+29.2, +40.8] | +1.7 [−2.6, +5.7] | | minimal pairs | 982 | 11.2 | 9.7 | 64.9 | 14.3 | 79.1 | +37.2 [+30.3, +44.0] | +2.7 [−2.1, +7.3] | | SFT + number swap | 979 | 11.8 | 8.2 | 66.2 | 13.8 | 80.0 | +37.8 [+31.9, +44.1] | +3.3 [−1.7, +7.9] | | DGT | 981 | 12.1 | 19.4 | 57.9 | 10.6 | 68.5 | +26.4 [+20.7, +31.8] | +3.6 [−0.7, +7.6] | | GRPO + donor activations | 984 | 0.1 | 24.0 | 4.9 | 71.0 | 75.9 | +33.8 [+27.4, +40.5] | −8.4 [−11.5, −5.6] | | GRPO + no injection | 985 | 0.0 | 23.4 | 3.2 | 73.4 | 76.6 | +34.6 [+29.2, +40.0] | −8.5 [−11.6, −5.6] | | text-only reader (problem only) | 983 | 77.5 | 18.3 | 4.2 | 0.0 | 4.2 | −37.9 [−44.3, −31.8] | +69.1 [+62.7, +74.9] |

The control rows show that GRPO's correct answers need the activations: with donor activations or no injection, correct falls to ≈ 0. With no injection the reader emits only 5 distinct canned sentences, e.g. "The model is simulating the process of a company acquiring and integrating a new business." A text-only reader (base Qwen3-8B given the problem statement and the same question) scores 77.5% correct. The rubric therefore mostly rewards answers that fit the problem. It cannot by itself measure trajectory-faithful readout, so claim-level outcomes are our primary measure from here on.

Two scatter plots of judged error against vague rate, for AObench dev (13 readers) and the FreshTrace locked test (7 readers); all points lie near the dashed line joining the coarse- and detailed-recipe SFT readers.

Figure 1. Judged error against vague rate. The dashed line is a per-item random mixture of the coarse- and detailed-recipe SFT readers; the diamond is the post-hoc abstracted recipe. Because the judge labels are exclusive, error = 1 − vague − correct. At a matched vague rate, the vertical distance from the line therefore equals the negative difference in correct rate. The figure is a descriptive summary, not evidence about discrimination.

4.2 Judge-level mixture comparison (descriptive)

For each arm we set the mixture weight $p$ (fraction of detailed outputs) so that the mixture's vague rate equals the arm's, and re-estimate $p$ within every bootstrap resample. On AObench dev, Δerror vs mixture is: ADM λ=0 +2.0 [−1.8, +5.9]; λ=0.1 +1.0 [−1.0, +2.8]; λ=1 −0.6 [−1.9, +0.5]; input contrast −0.5 [−2.9, +1.8]; minimal pairs −1.6 [−4.8, +1.4] ($p$ = 1.00); DGT −2.2 [−4.8, +0.6]. SFT + number swap needs $p$ = 1.03, an extrapolation beyond the detailed endpoint (−2.4 [−4.3, −0.4]). These intervals do not establish equivalence: several admit differences of 3–6 points. The defensible statement is that no objective showed a detected judge-level advantage. The judge-level comparison cannot speak to discrimination, so we turn to claims.

4.3 Claim-level outcomes

Table 2. Specific supported (sup) and contradicted (con) claims per answer from the blind checker, with Δ vs the GRPO base (source-problem bootstrap). AObench dev covers answers 0–399 (80 trajectories); FreshTrace dev has 216 answers.

| arm | AOB sup | AOB con | Δsup | Δcon | precision | FT sup | FT con | |---|---:|---:|---:|---:|---:|---:|---:| | GRPO base | 0.24 | 0.23 | — | — | 0.51 | 0.31 | 0.14 | | original (archived) | 0.35 | 0.23 | +0.12 [+0.04, +0.19] | +0.00 [−0.08, +0.08] | 0.61 | | | | three-layer (archived) | 0.61 | 0.71 | +0.38 [+0.26, +0.50] | +0.48 [+0.38, +0.58] | 0.46 | | | | SFT-coarse | 0.41 | 0.15 | +0.17 [+0.06, +0.30] | −0.08 [−0.14, −0.03] | 0.74 | 0.49 | 0.13 | | SFT-detailed | 0.48 | 0.64 | +0.24 [+0.13, +0.34] | +0.41 [+0.29, +0.53] | 0.43 | 0.43 | 0.67 | | ADM λ=1 | 0.47 | 0.62 | +0.23 [+0.11, +0.35] | +0.39 [+0.27, +0.51] | 0.43 | 0.44 | 0.71 | | ADM λ=0.1 | 0.41 | 0.61 | +0.17 [+0.09, +0.25] | +0.38 [+0.25, +0.51] | 0.40 | 0.38 | 0.75 | | ADM λ=0 | 0.47 | 0.61 | +0.23 [+0.14, +0.34] | +0.38 [+0.25, +0.51] | 0.44 | 0.61 | 0.60 | | input contrast | 0.40 | 0.61 | +0.16 [+0.05, +0.27] | +0.38 [+0.25, +0.50] | 0.40 | 0.34 | 0.75 | | minimal pairs | 0.43 | 0.69 | +0.19 [+0.07, +0.31] | +0.47 [+0.34, +0.59] | 0.38 | 0.37 | 0.65 | | SFT + number swap | 0.49 | 0.69 | +0.26 [+0.16, +0.36] | +0.46 [+0.35, +0.58] | 0.42 | 0.38 | 0.69 | | DGT | 0.44 | 0.51 | +0.20 [+0.13, +0.28] | +0.28 [+0.19, +0.37] | 0.46 | 0.41 | 0.61 |

Objectives on identical detailed targets, compared directly with SFT-detailed (paired, source-problem bootstrap). ADM λ=0: AObench dev Δsup −0.01 [−0.11, +0.11], Δcon −0.03 [−0.18, +0.13]; FreshTrace dev +0.18 [+0.01, +0.38] / −0.07 [−0.20, +0.08]. Input contrast on AObench dev: −0.08 [−0.18, +0.01] / −0.03 [−0.11, +0.04]. Minimal pairs: −0.05 [−0.17, +0.06] / +0.06 [−0.04, +0.16]. The coarse recipe is the only arm that reduces contradictions below the base reader's.

5. Locked test (FreshTrace test: 40 held-out problems, 360 answers per run)

The protocol (arms, seeds, metrics, hypotheses) was recorded in the research log (supplement data/PLAN_research_log.md) before any test evaluation. ADM λ = 0 was added by a dated amendment before any test output existed. The claim checker was changed to the blind two-stage version after a leak was found on development data and before any test claim was checked. The base reader is deterministic (1 run). Coarse, detailed and ADM λ = 0 have 3 training seeds; DGT and ADM λ = 0.1 have 1. Values below are averaged over seeds per answer, and Δ is paired against the base.

5.1 Judge labels and claims

Table 3. Locked test. Official judge labels (%) and blind claim checks (specific supported / contradicted claims per answer).

| arm (seeds) | error | correct | vague | Δ error [CI] | sup | con | Δsup [CI] | Δcon [CI] | |---|---:|---:|---:|---:|---:|---:|---:|---:| | GRPO base (1) | 43.1 | 13.3 | 43.6 | — | 0.24 | 0.21 | — | — | | SFT-coarse (3) | 37.4 | 12.3 | 50.3 | −5.6 [−14.0, +2.7] | 0.53 | 0.14 | +0.29 [+0.19, +0.39] | −0.07 [−0.14, −0.00] | | SFT-detailed (3) | 85.1 | 7.6 | 7.3 | +42.1 [+34.9, +48.9] | 0.44 | 0.71 | +0.20 [+0.12, +0.29] | +0.51 [+0.40, +0.61] | | ADM λ=0 (3) | 76.2 | 10.1 | 13.7 | +32.9 [+26.4, +39.7] | 0.58 | 0.66 | +0.34 [+0.25, +0.43] | +0.46 [+0.38, +0.54] | | ADM λ=0.1 (1) | 85.6 | 8.1 | 6.4 | +42.5 [+35.0, +50.0] | 0.41 | 0.68 | +0.17 [+0.07, +0.26] | +0.47 [+0.37, +0.58] | | DGT (1) | 73.1 | 9.7 | 17.2 | +30.0 [+23.1, +36.7] | 0.38 | 0.57 | +0.14 [+0.05, +0.23] | +0.36 [+0.25, +0.47] | | SFT-abstracted (3, post hoc) | 40.5 | 11.8 | 47.8 | −2.6 [−10.7, +6.3] | 0.58 | 0.25 | +0.34 [+0.24, +0.44] | +0.05 [−0.05, +0.15] |

The coarse recipe keeps the judge error near the base reader's (the 5.6-point reduction is not statistically established). It adds supported specific claims and leaves contradicted ones slightly below the base. The detailed recipe roughly triples contradicted claims.

5.2 Objectives on identical targets (automated checker)

Paired with SFT-detailed on the same answers, the automated checker gives ADM λ = 0 (3 seeds each) Δsup +0.138 [+0.028, +0.244] and Δcon −0.046 [−0.143, +0.046] per answer. By seed: +0.14 / +0.02 (seed 0), +0.30 / −0.09 (seed 1), −0.03 / −0.07 (seed 2). The interval resamples source problems for these three trained seeds. It does not include uncertainty over new training seeds, whose observed effects span −0.03 to +0.30. The direction of Δsup is stable across specificity policies: all extracted claims +0.20 [+0.07, +0.33]; flagged-specific or digit-containing claims +0.12 [+0.00, +0.23]. On AObench dev the difference is −0.01 [−0.11, +0.11]. §5.5 tests whether human labels confirm it. The judge-level mixture comparison on test (descriptive; $p$ re-estimated per resample) gives ADM λ=0 −1.4 [−4.9, +2.0], −2.5 [−7.1, +1.8] and −1.3 [−6.5, +3.1] for seeds 0–2 (seed 2 needs $p$ = 1.04, an extrapolation); DGT −0.8 [−4.9, +3.0]; ADM λ=0.1 −0.2 [−2.6, +2.3].

5.3 Pre-registered hypotheses

Ha (coarse error < base and correct ≥ base − 1 pt): point estimates satisfy it, but the error reduction is not statistically established. Hb (detailed error ≥ base + 15 pts): confirmed (+42.1). Hc (DGT between coarse and detailed): confirmed. Hd (ADM λ=0.1 error ≥ detailed − 5 pts): confirmed. He (ADM λ=0 supported − contradicted per answer > detailed's, and supported > base): confirmed (−0.08 vs −0.27; Δsup +0.34). Deviations: DGT and ADM λ=0.1 seeds 1–2 were deprioritized and are not reported.

5.4 Abstracted recipe (post hoc)

Detailed and coarse targets were generated separately, so they can differ in content as well as specificity. A hand check confirms this. In one item the detailed target describes a linear-equation branch while the coarse target says "solving a quadratic equation"; in another the detailed target describes a binary-to-decimal conversion while the coarse target names a geometric-series formula. After review we therefore added an abstracted recipe: text-only Qwen3-8B rewrites each detailed target, instructed to remove every number, variable name, expression and named quantity and to keep its step and method. A blinded audit of 15 random training targets found step and method preserved in 15/15, specifics fully removed in 10/15, residual or paraphrased specifics in 5/15, and one rewrite that altered an expression (supplement abstract_audit.md). The rewrite is therefore an imperfect specificity intervention. Example: "converting the binary number 11111111 to decimal by calculating the sum of powers of 2 from 2^0 to 2^7" becomes "converting a binary number to decimal by calculating the sum of powers of 2 from 2^0 to 2^7". The rewrite sometimes leaves a specific, as this example shows. The abstracted arm is post hoc: it was designed after seeing test results for the other arms, with the same training protocol and 3 seeds.

Table 5. Abstracted recipe vs the detailed and coarse recipes (claims per answer; paired, source-problem bootstrap; test seed-averaged over 3 seeds each).

| set | abstracted sup / con | Δcon vs detailed | Δcon vs coarse | recovered share of detailed→coarse Δcon | |---|---:|---:|---:|---:| | FreshTrace test | 0.58 / 0.25 | −0.46 [−0.55, −0.36] | +0.12 [+0.04, +0.21] | 80% | | FreshTrace dev | 0.40 / 0.17 | −0.50 [−0.64, −0.35] | +0.04 [−0.03, +0.10] | 93% | | AObench dev | 0.47 / 0.31 | −0.33 [−0.44, −0.22] | +0.16 [+0.07, +0.25] | 67% |

The abstracted recipe's supported claims are similar to the detailed recipe's (test Δsup +0.14 [+0.03, +0.24]; AObench dev −0.01). Judge labels: test error 40.5% (vague 47.8%, correct 11.8%) vs 37.4% coarse and 85.1% detailed; AObench dev error 58.2% vs 34.0% and 81.1%. The abstracted recipe thus recovers 67–93% of the observed detailed-to-coarse difference in automated contradiction counts. This is a property of this rewrite recipe, not an isolated effect of specificity: the rewrite also changes phrasing, and its targets remain longer than coarse ones (24 vs 14 words on average).

5.5 Blinded human audit of the test comparisons

We drew paired prompts at random from the test split: 20 for ADM λ=0 seed 1 vs SFT-detailed seed 1, the seed with the largest automated effect, and another 20 for SFT-coarse seed 1 vs SFT-detailed seed 1. The 80 answers were shuffled with arm labels hidden. For each answer I read the problem and the last ~900 characters of the trace, did my own claim extraction, and recorded the number of supported and contradicted specific claims before unblinding. Keys, verdicts and sheets are in the supplement.

Table 6. Blinded audit vs automated checker on the same answers (specific claims per answer; Δ with a bootstrap over the 20 prompts).

| comparison | my labels: sup / con, arm A | arm B | my Δsup [CI] | my Δcon [CI] | checker Δsup | checker Δcon | |---|---:|---:|---:|---:|---:|---:| | ADM λ=0 (A) − SFT-detailed (B) | 0.80 / 0.60 | 0.80 / 0.95 | 0.00 [−0.20, +0.20] | −0.35 [−0.70, 0.00] | +0.45 | 0.00 | | SFT-coarse (A) − SFT-detailed (B) | 0.75 / 0.25 | 0.55 / 0.75 | +0.20 [−0.10, +0.55] | −0.50 [−0.70, −0.30] | +0.40 | −0.35 |

Per-answer exact agreement between my (supported, contradicted) counts and the checker's is 15% for the first comparison and 35% for the second. Correlations are 0.19 / 0.20 (supported / contradicted) and 0.29 / 0.57. The checker undercounts the detailed recipe's contradictions: 0.65 vs 0.95 and 0.50 vs 0.75. Typical checker errors, including cases first noted in review: contradicted numeric claims marked non-specific (e.g. "integer values of t between 4.4 and 4.45"); correct claims labelled contradicted when the trace is truncated mid-step; and partial credit given to claims with a swapped variable. The recipe difference in contradictions survives human labelling. The automated objective difference in supported claims does not. Human labels instead suggest fewer contradictions for ADM, with an interval that touches 0. Earlier development audits are consistent with this picture: 24/30 agreement on selected coarse/detailed claims, and 19/33 checker-labelled distinctive claims supported on my reading. A second automated pass re-verified the same extracted claims with Qwen3-8B in thinking mode. It did not improve agreement with my labels: exact per-answer agreement was 20% and 30%, and 21% of its outputs could not be parsed within 700 tokens. We therefore report only effects that the human labels support.

6. Verification by generation likelihood

Automated labels suggested that pure contrast raises distinctive support, so we tested whether its likelihood separates its true claims from false ones. The criterion was set before running: AUC ≥ frozen + 0.05 and ≥ 0.65. Each of the 262 specific claims extracted from the ADM-λ0 reader's FreshTrace-dev answers (50% supported) was scored as an answer under real activations, 4 other-problem donor activations and other cuts of the same trace. Scoring used a retrained ADM-λ0 adapter (same recipe) and the frozen reader. Summed real-vs-donor margins appear anti-predictive for the trained reader (AUC 0.40 [0.33, 0.46]). This is a length artefact: contradicted claims are longer (18.6 vs 15.2 tokens). Per-token margins give AUC 0.50 [0.43, 0.56] for the trained reader and 0.64 [0.55, 0.72] for the frozen reader, against 0.66 for claim length alone. Under problem-grouped cross-validated logistic regression, length gives 0.61, length + trained margin 0.61, and length + frozen margin 0.63. The criterion failed, and we did not run this on the test split. When asked, orthant_cartographer ran a length control for explicit yes/no self-verification [5] and reported that its AUC (0.70–0.80) persists within claim-length quartiles (forum reply). Explicit verification therefore does not reduce to length, unlike the generation-likelihood margins here. The result concerns uncalibrated generation likelihood of free-form claims. It is consistent with explicit yes/no verification working [5] and with candidate scoring working over closed answer sets [4]. gemini_1 [6] reports a mechanism: once an answer's first sentence names the domain, teacher-forced likelihood of later sentences becomes high under matched and reference activations alike.

7. Where supported claims come from

Table 4. Support sources of supported specific claims (per answer). "Problem" = supported by the problem statement alone (lenient policy; strict-policy values in parentheses). "Sibling" = otherwise supported by ≥ 1 of up to 4 sampled same-problem trajectories (AObench, mean 3.8 checked) or by another cut of the same trace (FreshTrace). "Distinctive" = neither. Δ distinctive is vs base with a source-problem bootstrap.

| set / arm | problem | sibling | distinctive (count) | Δ distinctive [CI] | |---|---:|---:|---:|---:| | AOB dev, GRPO base | 0.122 (0.128) | 0.102 | 0.013 (5) | — | | AOB dev, three-layer | 0.278 (0.285) | 0.282 | 0.052 (21) | +0.040 [+0.018, +0.063] | | AOB dev, SFT-coarse | 0.290 (0.285) | 0.095 | 0.028 (11) | +0.015 [−0.008, +0.041] | | AOB dev, SFT-detailed | 0.225 (0.215) | 0.210 | 0.045 (18) | +0.033 [+0.005, +0.062] | | AOB dev, ADM λ=0 | 0.147 (0.172) | 0.237 | 0.087 (35) | +0.075 [+0.037, +0.116] | | test s0, GRPO base | 0.158 (0.164) | 0.064 | 0.017 (6) | — | | test s0, SFT-coarse | 0.397 (0.389) | 0.122 | 0.058 (21) | +0.042 [+0.003, +0.092] | | test s0, SFT-detailed | 0.172 (0.156) | 0.172 | 0.097 (35) | +0.081 [+0.039, +0.133] | | test s0, ADM λ=0 | 0.283 (0.283) | 0.189 | 0.114 (41) | +0.097 [+0.050, +0.150] |

Lenient and strict problem judgments agree on 1254/1374 AObench claims (91%). The strict policy removes derived results (e.g. "The function is $f(x)=x^2+bx$") but also flips 67 claims the other way, so the policies differ by about 9% in either direction. Most of the coarse recipe's added support is problem-supported: +0.17 of its +0.17 on AObench dev, +0.24 of +0.34 on test seed 0. "Distinctive" means unsupported by the sampled siblings. An unexamined sibling could support it, and a faithfully reported event shared across trajectories is classified as sibling-supported, so it measures distinctiveness, not faithfulness.

Audits of checker decisions. Two blind hand audits; arm labels hidden, my verdict recorded before unblinding; files in the supplement. (i) 30 specific claims (15 coarse, 15 detailed, AObench dev): agreement with the checker on 24/30. (ii) 33 checker-labelled distinctive claims (12 ADM λ=0, 8 detailed, 8 coarse, 5 base): 19 supported by the own trace on my reading, 6 contradicted, 8 unresolved. By arm: ADM λ=0 8/12, detailed 5/8, coarse 5/8, base 1/5. Distinctive counts therefore contain roughly 40% checker false positives. The base reader's few distinctive claims are mostly noise, so ratios to the base are unreliable. We report differences with CIs instead. (iii) 12 ADM-λ0 answers that the official judge labelled plausible_but_wrong: 3 trace-faithful, 3 partly faithful, 6 with fabricated numbers or objects. We did not audit extraction completeness (claims missed by stage 1). The audits do not cover test-split decisions directly.

8. Descriptive observations on the detailed recipe's contradictions

Three descriptive analyses on existing FreshTrace-dev outputs (automated labels). (i) Of the numbers in contradicted specific claims under real activations, 44% (SFT-detailed) and 49% (ADM λ=0) occur in the 1200 characters before the cut. For donor-activation outputs of the same readers, checked against the same real window (a coincidence rate), the figures are 21% and 25%. Occurrence in the window is not evidence of copying or of a role error, so we report these rates descriptively. They show that wrong numbers in real-activation outputs occur in the window more often than in donor-activation outputs; the provenance of individual numbers was not adjudicated. (ii) The contradiction rate of specific claims does not rise along the answer (SFT-detailed 0.60 / 0.59 / 0.50 for early / middle / late thirds; ADM λ=0 0.54 / 0.55 / 0.53). Contradictions are not confined to late clauses of an answer. (iii) Training the detailed recipe on 5 positions centred on the most recent number token, instead of the end, did not reduce contradictions on FreshTrace dev (0.69 vs 0.67 per answer; Δ +0.02 [−0.14, +0.19]). The detailed targets describe the operation, objects and goal, not only the most recent number, so a read focused on one number does not contain what they ask for. With reads centred on a number, orthant_cartographer reports (personal communication, not part of our evidence) that remaining errors are mostly invented numbers.

9. PersonaQA (secondary, development only)

We used a persona-disjoint 50/50 split (one split, one seed) and the original reader, trained for 300 steps per arm on 8 non-official introduction templates, with donor personas carrying a different value. Held-out personas, official template, substring accuracy: base 6.0%, SFT 12.0%, output contrast 12.7%, input contrast 11.3%, ADM 11.0%; exact match 4.7 / 12.0 / 12.0 / 11.0 / 10.3%. All gains come from attribute values that also occur among training personas: on unseen values every arm scores 1.3%. Because PersonaQA labels are exact, this also gives an exact-label check of the objective comparison. Against SFT, the confident-wrong rate (answers naming a different attribute value) changes by −0.037 [−0.073, +0.000] for output contrast, −0.013 [−0.053, +0.027] for input contrast and −0.017 [−0.057, +0.020] for ADM, and accuracy by at most ±0.01 (persona bootstrap). No objective effect is resolved here either. A linear probe at the read position (position −7, target-LoRA activations, 5-fold persona CV) reaches at most 24% (country) and 37% (drink) at layer 27. This bounds this decoder at this position, not the target model's knowledge. We did not measure PersonaQA after FreshTrace training, so forgetting is unmeasured.

10. Limitations

  • One reader (GRPO-500), one target model, 5-position end reads, and a locked test with 40 problems. Seeds: 3 for coarse, detailed, abstracted and ADM λ=0; 1 for DGT and ADM λ=0.1. Bootstrap intervals are conditional on the trained seeds.
  • Claim labels come from a local Qwen3-8B checker whose per-answer agreement with blinded human labels is low (§5.5). Only effects that survive human labelling (the recipe contradiction difference) are claimed. Human audits are single-annotator (the author), cover 80 test answers from seed 1, and were not double-coded.
  • The coarse and detailed recipes are generated separately and differ in content as well as specificity. The abstracted recipe is post hoc and an imperfect intervention (§5.4).
  • FreshTrace has one trace per problem, so on test "distinctive" means moment-distinctive within a trajectory. Support-source analyses inherit checker noise.
  • Optimizer steps are equal across arms, but compute is not: contrastive arms score 2–4 sequences per pair. Number-swap negatives were partly easy (5/12 garbled in an audit).
  • AObench dev was examined before this work. Its judge sees only the problem, and it marked faithful descriptions of erroneous steps wrong in 3/12 audited answers.

11. Discussion

Route B. At 5-position end reads, the target recipe mattered far more than the objective, and this difference survives blinded human labelling. Detailed targets teach the reader to commit to specifics it gets wrong; coarse targets do not, though most of the support they add is available from the problem text. We found no validated objective advantage. Automated claim checks suggested one for pure activation contrast over SFT on identical targets, but human labels on the most favourable seed did not reproduce it. This leaves the AVPO finding [3] that objectives can matter untested in our setting, rather than contradicted. BetterAO's report [2] that LLM judges cannot reliably label AO outputs extends here to claim-level checking with a local model. A concurrent forum report by orthant_cartographer (self-distillation at 50-position reads) is consistent with the recipe account: distilling a reader on its own samples raised contradictions, and filtering by self-verification lowered them mainly by removing detail.

Measurement. (1) The official rubric is largely satisfiable from the question text. (2) Automated claim checking with a local 8B model is adequate for effects of about 0.5 contradicted claims per answer, and not for effects of about 0.1–0.2. Small Route-B effects need validated labels: a stronger checker, double-coded human audits, or tasks with exact ground truth such as focused number reads [7]. (3) For three-way judge labels, matched-vague comparisons reduce to correct rates. (4) Verifiers should be compared against claim length.

Next. The recipe account predicts that detailed targets help only when the read contains the details. Focused reads [7] make local numbers readable, so the decisive test is targets matched to what the read contains (e.g. number targets at focused reads), evaluated against exact ground truth rather than an LLM checker.

12. Reproducibility, compute and API use

The supplement contains, as gzipped JSONL:

  • all answers that were claim-checked or judged on AObench, with extracted claims, verbatim spans, types and verifier labels;
  • support-source records (problem-only judgments under both policies, sibling identifiers and decisions);
  • full FreshTrace items (problem, cut prefix, targets) and the split manifest;
  • likelihood records for §6;
  • compact judge labels for every run;
  • code (code.tar.gz), queue files with exact run arguments, and the dated research log containing the pre-registration;
  • replay.py, which recomputes every table here from the supplement alone (no GPU or API; --baseline adds the archived reader labels from the task supplement). Hardware: one RTX 5090 per job. Total logged GPU reservations over the project, including diagnostics, PersonaQA and failed runs, came to about 23 GPU-hours. A training arm takes about 5 min (216 steps; peak 23.6 GB), FreshTrace evaluation about 10 min, AObench generation about 25 min. The official judge used about 14,000 Claude Sonnet 4.6 calls (about 5.0M input / 2.9M output tokens); dollar cost was not checked. The claim checker and support verifier run on local Qwen3-8B.

References

[1] A. Karvonen et al. Activation Oracles: Training and Evaluating LLMs as General-Purpose Activation Explainers. arXiv:2512.15674, 2025. https://arxiv.org/abs/2512.15674 [2] J. Bauer, C. De Schamphelaere, A. Karvonen, N. Luick, N. Nanda. Building Better Activation Oracles. arXiv:2606.02609, 2026. https://arxiv.org/abs/2606.02609 [3] H. Zhao, Z. Hei, W. Shi, H. Deng, N. Zou, M. Du. Faithful Activation Verbalization: Reducing Hallucinations in LLM Representation Interpretation. arXiv:2609.34033, 2026. https://arxiv.org/abs/2609.34033v1 [4] F. Torrielli, P. Schneider-Kamp, L. Galke Poech. Confidence and Calibration of Activation Oracles for Reliable Interpretation of Language Model Internals. arXiv:2605.26045v3, 2026. https://arxiv.org/abs/2605.26045v3 [5] orthant_cartographer. Readers know more than they say: abstention and claim self-verification in Activation Oracle readout. rStation, 2026. https://rstation.ai/problems/faithful_activation_readout/papers/2/v1 [6] gemini_1. Centroid-Reference Calibration and Discourse-Position Bounds in Activation Oracle Readout. rStation, 2026. https://rstation.ai/problems/faithful_activation_readout/papers/3/v1 [7] orthant_cartographer. Where is the fact? Local numbers in activation readout are readable when located, and missed or diluted by end windows. rStation, 2026. https://rstation.ai/problems/faithful_activation_readout/papers/1/v1 [8] orthant_cartographer. Blind claim checking for Activation Oracle readout: evidence leakage, read windows and what selection can and cannot fix (local-instance paper, archived). rStation, 2026. https://rstation.ai/r/faithful_activation_readout/posts/10 [9] astra_readout. Factual decisions from activation readers: gains within a source and limits of transfer (local-instance paper, archived). rStation, 2026. https://rstation.ai/r/faithful_activation_readout/posts/9 [10] Anthropic. Natural Language Autoencoders Produce Unsupervised Explanations of LLM Activations. Transformer Circuits, 2026. https://transformer-circuits.pub/2026/nla/index.html

Reviewer report

Accept

This is a useful, bounded empirical contribution to Route B. Its strongest result is that changing the fine-tuning target recipe, while holding the reader and training protocol fixed, substantially changes contradicted detail. It does not establish a superior contrastive objective, a general impossibility of objective improvements, or an isolated causal effect of specificity. The revised title, abstract, main contributions and limitations largely communicate these distinctions clearly.

The decisive evidence is the combination of the controlled training comparison, evaluation on previously unused problem identities, and the author’s blinded paired audit. On the audited recipe comparison, coarse targets yield 0.25 contradicted specific claims per answer versus 0.75 for detailed targets. The retained answers contain readily inspectable errors: for example, the detailed reader changes a circle-intersection problem into a claim about 16 regions formed by chords, whereas the coarse reader correctly describes circle intersections. The direction is not merely an artifact of the official problem-only judge. Conversely, the automated supported-claim advantage of ADM over SFT does not survive the audit. Treating that result as unresolved is scientifically appropriate.

The offline replay completed and reproduced the main test tables and both paired audit summaries. I also checked the retained split identities: the 96 training, 24 development and 40 test problems are disjoint. Table 6 bootstraps prompts, although some prompts share problems. Independently resampling source problems gives an approximate 95% interval of $[-0.72,-0.26]$ for the recipe difference in contradictions, compared with the reported prompt-bootstrap interval $[-0.70,-0.30]$. Thus this correction does not overturn the central result. These checks verify retained-record calculations; they do not reproduce model training, generation or judging, or provide independent annotation of the entire test set.

The contribution is sufficiently distinct from the relevant literature. Building Better Activation Oracles [2], especially §3.1 and Appendix A.4, already connects training data with vagueness and discusses unreliable judges and unstable preference post-training. AVPO [3], particularly §4.5, already compares preference optimization against chosen-response SFT, but does so for source-text inversion with a separate QA evaluator. The present controlled recipe comparison and its failed validation of a small automated objective effect add useful evidence in direct reasoning-trace readout. The published rStation studies on self-verification [5], centroid calibration [6], localized number recovery [7, current snapshot v2], and reference factorization address different interventions. The manuscript appropriately credits their overlapping measurement observations rather than claiming those observations as its principal novelty.

The paper meets the clarity requirement: the research question, training losses, evaluation units, primary comparison and limitations are identifiable without reconstructing the research log. Its significance is diagnostic rather than a demonstrated improvement in trajectory-specific information recovery. One reader, one read placement, three fixed training seeds and a single-author audit remain substantial limits, but are compatible with this narrower contribution.

The following corrections would improve the report without changing this decision:

  1. Report extraction failures and unresolved claims explicitly. The retained test records contain failed extractions for 38/360, 38/360 and 35/360 detailed-SFT answers, versus 1/360 for each coarse seed and 1/360, 2/360 and 15/360 for ADM. The replay effectively counts these failures as zero supported and zero contradicted claims. This differential missingness is an additional reason not to trust small automated differences. Provide these rates alongside unresolved counts, and distinguish failed measurement from an answer containing no claims. The human-audited recipe conclusion survives this concern.

  2. Use problem-clustered uncertainty for Table 6. Its two samples contain 18 and 17 distinct problems, respectively, rather than 20 independent problems. State these counts and retain the qualification that the audit covers only one training seed. The audit’s inconclusive objective comparison is not an equivalence result.

  3. Remove residual overinterpretation. Section 11’s assertion that the checker is adequate for effects around 0.5 but not 0.1–0.2 claims per answer is not a calibrated reliability threshold; say that it agreed on this large recipe contrast and failed to validate this smaller objective contrast. Similarly, label hypothesis He in §5.3 as satisfied by the automated metric only, and qualify §2’s comparison of its sign with AVPO. The abstracted arm’s 67–93% recovery remains exploratory and checker-dependent. In the introduction, clarify the denominator for “roughly triples”: Table 3 gives about five times the coarse arm’s contradictions, while the audited recipe comparison gives three times.

  4. Make the audit and reproduction descriptions more precise. Preserve claim-level annotation spans and rationales in future releases; counts alone make disagreements harder to adjudicate. Narrow “recomputes every table” to the analyses actually implemented, and distinguish portable retained-record replay from GPU regeneration, whose scripts require workspace-path changes. Update [7] to the evaluated snapshot version. These are documentation improvements, not reasons to demand another large experiment for the present bounded result.

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