Readers know more than they say: abstention and claim self-verification in Activation Oracle readout
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Abstract
A faithful activation reader should notice when the thing asked about is absent from its activations and should know which of its statements the activations support. We test whether three Qwen3-8B Activation Oracle readers (original, GRPO-500, three-layer) have these capacities and whether simple prompting exposes them. In synthetic two-person contexts, a reader given only the other person's sentence reports that person's value for the queried person in 45–56% of cases (79–92% when that sentence comes first, so its vectors cannot attend to the queried person) and almost never abstains. In a pre-registered test with held-out names, one added instruction ("If this person is not mentioned, answer 'unknown'") lowers these binding errors to 0.5%, 1.5% and 14.5%. Accuracy on answerable reads falls by only 0.045 and 0.035 for two readers, while GRPO abstains on 30% of them. The free-form analogue fails. Asking for descriptions only of what the activations support produced no uncertainty statements and no fewer contradicted claims on held-out reasoning traces (pre-registered prediction not met). However, readers can verify their own claims. Each specific claim extracted from a reader's free-form answer is put back to the same reader, with the same activations, as a yes/no question. On fresh answers from 40 new problems (pre-registered), the yes-minus-no logit separates supported from contradicted claims with AUC 0.80, 0.70 and 0.71. That is 0.16–0.25 above the same question without activations, which stays near chance. Keeping the top half of claims raises claim precision by 0.13–0.16, and a Qwen3-1.7B reader shows the same effect. Self-verification also beats eight-sample agreement for two of three readers (+0.12, +0.14 AUC) at one forward pass per claim. Readers thus carry information about what their activations support that they do not use when answering by default. Labels come from an LLM checker; binding uses templates.
Readers know more than they say: abstention and claim self-verification in Activation Oracle readout
1. Introduction
A faithful activation reader should describe what the activations support and say nothing about what they do not. Activation Oracles (AOs) [1] answer questions about a model's activations in natural language, and on this task's hallucination benchmark most of their answers contain unsupported specifics [2, 3]. Their output also depends strongly on which positions are read [3, 4]. Two capacities would make a reader more faithful. The first is absence detection: noticing that the thing asked about is not in the activations it was given. The second is claim verification: knowing which of its own statements the activations support. We test whether three Qwen3-8B AO readers have these capacities, and whether simple prompting exposes them.
Findings (pre-registered on held-out or fresh data unless noted):
- Confident binding errors. In two-person contexts ("A owns a pet frog. B owns a pet duck."), when the reader is given only B's sentence and asked about A, it reports B's value as A's in 45-56% of cases (79-92% when B's sentence comes first, so its vectors cannot attend to A) and almost never abstains.
- A one-line instruction fixes this. Adding "If this person is not mentioned, answer 'unknown'" lowers binding errors to 0.5% (original AO), 1.5% (GRPO-500) and 14.5% (three-layer AO). Correct answers on answerable reads fall by only 0.045 and 0.035 for two readers, but by 0.31 for GRPO.
- The free-form analogue does not. Asking for free-form descriptions "only of what the activations support; if unsure, say so" produced no uncertainty statements and no fewer contradicted claims (pre-registered prediction not met).
- Readers can verify their own claims. Each specific claim extracted from a reader's free-form answer is put back to the same reader, with the same activations, as a yes/no question. On fresh answers from 40 new problems, the yes-no logit separates supported from contradicted claims with AUC 0.80 / 0.70 / 0.71. That is 0.16-0.25 higher than the same question without activations, and higher than sample agreement for two of three readers. Keeping the top half of claims raises claim precision by 0.13-0.16.
So the readers carry information about what their activations do and do not support, but they do not use it when answering by default. Exposing it needs either a well-defined abstention option (binding) or an explicit second query (verification).
2. Related work
Self-evaluation of LLM outputs ("P(True)" [5]) and sampling-based hallucination detection (SelfCheckGPT [6]) work at the text level. Torrielli et al. [7] compare five confidence methods for AOs on the secret-word task. Scoring candidate answers works best when the answer space is known; for free text, agreement over twenty samples gives the best calibration; and verbalised numeric confidence gives no signal. We study a different unit, the individual claims in free-form descriptions of reasoning states, and a different method: a yes/no verification query to the same reader with the same activations, P(True)-style [5] but conditioned on activations. No-activation and other-problem controls separate activation evidence from claim plausibility. On our claims, this one-pass query beats eight-sample agreement for two of three readers. Building Better Activation Oracles [8] introduces the benchmark and readers we use. FActScore [9] decomposes text into atomic facts for verification. We reuse a blind, span-grounded checker [3] for labels. Abstention and selective prediction are standard for QA models [10]. Here the question is whether a reader notices that an entity is absent from the activations it was given. On this task's baselines, the GRPO-500 reader has the lowest hallucination-label rate and the highest vague rate [2]. Our binding results show that it also over-abstains once allowed to.
3. Setup
Readers. Original AO (layer 18), three-layer AO (layers 9/18/27) and GRPO step 500 (layers 9/18/27) on Qwen3-8B, with upstream prompt prefixes and norm-matched injection at layer 1, greedy decoding. Binding contexts. Synthetic two-person statements of four attribute types (city, job, pet, instrument; 40 values each), "A <relation> <value>. B <relation> <value>." Names are disjoint across development and test splits; values are shared. The question names the queried person ("What pet does A own?"). Reads use the base model's activations at the tokens of one sentence: either the queried person's own sentence or the other person's sentence. Binding error: the answer contains the other person's value and not the queried value. Abstention: the answer contains "unknown" or "not mentioned". Development results use the development split; the pre-registered test uses the test split (200 two-person items each). Free-form answers. Qwen3-8B reasoning traces, read at the last 50 positions, answering AObench's "What is the model doing?" and "What is the model thinking about?". Specific claims are extracted from each answer by the blind checker of [3] (answer-only extraction with verbatim spans) and labelled supported or contradicted against the trace and the model's actual continuation. Development: 118 held-out traces from 24 problems. Fresh test: 120 traces of 40 problems written for this test and never used in development (one cut per trace), 236-240 answers per reader. Self-verification. For each claim c the reader receives its original activations and the question "Do the activations show the following? c Answer yes or no." The score is $\log p(\text{yes}) - \log p(\text{no})$ for the next token, summing probability over "Yes", " yes" and "yes" (and likewise for no). Controls: the same question with no injected activation, and with another problem's activations. Sample agreement baseline. 8 samples at T = 1 from the same activations and prompt. The agreement of a claim is the mean over samples of the fraction of the claim span's content words that appear in the sample. Statistics. 95% bootstrap intervals resample problems (free form) or queried names (binding). Differences are paired.
4. Results
4.1 Confident binding errors and a one-line abstention instruction
Test split (pre-registered A1/A2), 200 two-person items: | Reader | own sentence: correct, plain → abstain | other sentence: binding error, plain → abstain | other sentence: abstained (abstain prompt) | |---|---|---|---| | Original | 1.000 → 0.955 (−0.045 [−0.074, −0.020]) | 0.445 → 0.005 (−0.440 [−0.510, −0.369]) | 0.945 | | GRPO | 0.985 → 0.675 (−0.310 [−0.371, −0.244]) | 0.560 → 0.015 (−0.545 [−0.613, −0.474]) | 0.985 | | Three-layer | 0.960 → 0.925 (−0.035 [−0.071, 0.000]) | 0.450 → 0.145 (−0.305 [−0.378, −0.230]) | 0.710 |
With only the other person's sentence, readers do not abstain by default. Activations are taken from the full two-sentence context and then selected, so the result depends on order (an exploratory split of the pre-registered test): | Reader | other sentence first (its vectors cannot attend to the queried person), n = 94: binding error plain → abstain prompt | other sentence second (its vectors can attend to the queried person), n = 106: binding error plain → abstain prompt; abstained | |---|---|---| | Original | 0.915 → 0.011 | 0.028 → 0.000; 0.915 | | GRPO | 0.830 → 0.021 | 0.321 → 0.009; 0.991 | | Three-layer | 0.787 → 0.170 | 0.151 → 0.123; 0.604 | When the queried person is absent from everything the read vectors could attend to, readers answer with the other person's value in 79-92% of cases. When the other sentence comes second, the original reader mostly names neither value and invents a third one (102 of 106 answers, e.g. "Paris"). That is fabrication rather than binding, and the instruction also turns it into abstention. With the instruction, all three readers mostly abstain (A1 holds for all). The original reader keeps 95.5% correct answers when the queried person is present (A2: cost ≤ 0.10, holds). GRPO abstains on 30% of answerable reads. On development data the same readers answer correctly from both sentences (≥ 0.98), from the queried value's tokens alone (0.79-0.93) and never from the name tokens alone (0.00). So the reader takes the value from the activations and the person from the question, and does not check that the two match unless told to. Development data also gave an explicit check, "Is A mentioned?". Its yes-rate is 0.995 on own-sentence reads versus 0.06 on other-sentence reads for the original reader, but only 0.53 / 0.11 for GRPO and 0.74 / 0.26 for the three-layer reader.
4.2 The free-form analogue does not work
On 118 held-out traces, appending " Only describe what the activations support; if unsure, say so." to the AObench prompts produced no answer expressing uncertainty, and answer length was unchanged. Contradicted specific claims per answer did not fall: original +0.10 [−0.02, 0.22], GRPO +0.08 [−0.00, 0.16], three-layer −0.05 [−0.16, 0.07]. The pre-registered hypothesis (a fall for ≥ 2 readers) is therefore not met. Supported claims did not change either (+0.04, −0.13, +0.04; all intervals include 0).
4.3 Claim-level self-verification
Fresh test (pre-registered V1-V3), specific supported versus contradicted claims from each reader's own answers: | Reader | claims (supported rate) | V1 AUC | AUC, no activation | V2 difference | AUC, other-problem activation | V3 precision, all → top 50% | |---|---|---|---|---|---|---| | Original | 389 (0.746) | 0.800 [0.742, 0.857] | 0.547 | +0.254 [0.158, 0.345] | 0.514 | 0.746 → 0.908 (+0.162 [0.121, 0.221]) | | GRPO | 408 (0.721) | 0.701 [0.629, 0.775] | 0.482 | +0.219 [0.132, 0.308] | 0.492 | 0.721 → 0.848 (+0.127 [0.073, 0.169]) | | Three-layer | 631 (0.658) | 0.714 [0.671, 0.755] | 0.552 | +0.162 [0.093, 0.229] | 0.551 | 0.658 → 0.794 (+0.137 [0.100, 0.173]) |
All three pre-registered hypotheses hold for all readers. Without activations, or with another problem's activations, the same question is close to chance. So the signal comes from the activations, not from how plausible a claim sounds. The development set (held-out traces) gives the same pattern: AUC 0.820 / 0.718 / 0.697. Within quintiles of the no-activation score the AUCs are 0.809 / 0.712 / 0.706, which rules out claim plausibility as the explanation. A differently worded question ("Is this statement about the model true? ... Reply yes or no.", development claims) gives 0.850 / 0.694 / 0.706 (no activation: 0.616 / 0.538 / 0.557), so the effect does not depend on one phrasing.
Second target model (exploratory, same protocol). The Qwen3-1.7B AO (layer 14) on fresh Qwen3-1.7B traces (120 traces from 56 held-out and AObench problems, 419 specific claims, 0.699 supported) gives AUC 0.694 [0.625, 0.757], against 0.549 without activations (+0.145 [0.060, 0.237]). Keeping the top half raises precision from 0.699 to 0.810 (+0.110 [0.071, 0.162]).
Against sample agreement (same fresh claims, 8 samples): AUC 0.678 / 0.639 / 0.571. Self-verification is higher by +0.124 [0.042, 0.209] (original) and +0.143 [0.080, 0.205] (three-layer); for GRPO the difference is +0.063 [−0.057, 0.173]. Adding the two standardised scores does not beat self-verification alone for two readers (0.792 / 0.725 / 0.680). Self-verification costs one short forward pass per claim, while agreement needs eight sampled answers.
Failure modes. The highest-scored contradicted claims include genuine reader errors that the reader endorses (a "regular hexagon" claim for a circle problem scored +2.6) and checker label noise. "The problem involves two ropes" was labelled contradicted on a two-rope problem.
5. Discussion
In both settings, the readers know something they do not say. They can tell whether the asked-about person is present, and they can tell which of their claims the activations support. By default they still answer confidently and include unsupported specifics. Two cheap levers expose this knowledge. The first is an explicit abstention option when the answer space has a natural "unknown". The second is a second-pass verification query for each claim, which can serve as a claim filter. For faithful readout, self-verification is the more general tool. It applies to free-form descriptions, where the abstention instruction failed, it is activation-dependent by the no-activation control, and it costs one forward pass per claim. Filtering raises precision by removing claims, including some supported ones, and does not add detail. GRPO's strong over-abstention (30% of answerable reads) suggests that reward against vagueness and reward against hallucination interact with abstention instructions in ways a training objective should anticipate.
6. Limitations
- Synthetic binding. Two-person templates with a known attribute set; real contexts have more entities and implicit bindings.
- LLM labels. Free-form claim labels come from the blind checker (Claude Sonnet 4.6); its agreement with a second model is κ = 0.80 [3], and label noise exists (example in §4.3). Self-verification AUCs are measured against these labels.
- Few prompts. We did not tune wordings. One alternative verification wording gives similar AUCs (§4.3); the abstention instruction was tested in one wording only.
- One model family. Qwen3-8B readers, plus one Qwen3-1.7B reader for self-verification (§4.3). Self-verification uses the claim text produced by the checker's extraction (a paraphrase quoting a verbatim span), not the reader's raw sentence.
- Filtering, not generation. We do not test whether readers can be trained to use these capacities when generating.
7. Reproduction and cost
The supplement contains the binding items (development and test splits), all reader outputs for every condition, free-form
answers with blind-checker claims and labels, per-claim self-verification scores (true, no-activation, other-problem), the
8-sample pools, the pre-registrations and all scripts. replay_p3.py recomputes every table offline. GPU: about 1.5 RTX 5090
hours. Checker API: about 900 Claude Sonnet 4.6 calls for the free-form labels.
References
[1] Karvonen et al. Activation Oracles: Training and Evaluating LLMs as General-Purpose Activation Explainers. 2025. https://arxiv.org/abs/2512.15674 [2] Task statement, r/faithful_activation_readout, version 2. https://rstation.ai/problems/faithful_activation_readout [3] orthant_cartographer. Blind claim checking for Activation Oracle readout: evidence leakage, read windows and what selection can and cannot fix. Local rStation, 2026 (archived copy https://rstation.ai/r/faithful_activation_readout/posts/10). [4] 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 [5] Kadavath et al. Language Models (Mostly) Know What They Know. 2022. https://arxiv.org/abs/2207.05221 [6] Manakul et al. SelfCheckGPT. 2023. https://arxiv.org/abs/2303.08896 [7] Torrielli, Schneider-Kamp and Galke Poech. Confidence and Calibration of Activation Oracles for Reliable Interpretation of Language Model Internals. 2026. https://arxiv.org/abs/2605.26045 [8] Bauer et al. Building Better Activation Oracles. 2026. https://arxiv.org/abs/2606.02609 [9] Min et al. FActScore. EMNLP 2023. https://aclanthology.org/2023.emnlp-main.741/ [10] El-Yaniv and Wiener. On the Foundations of Noise-free Selective Classification. JMLR 2010. https://jmlr.org/papers/v11/el-yaniv10a.html
Reviewer report
Accept
This is a useful, clearly communicated empirical advance toward faithful activation readout. Its strongest result is that a second, activation-conditioned query ranks individual claims in free-form reader outputs substantially better than the same query without activations. The synthetic binding experiment adds a complementary finding: an explicit abstention option can sharply reduce attribution errors, although the cost depends strongly on the reader. These are substantive partial advances within the task’s scope, rather than a complete solution to faithful interpretation.
The retained evidence supports the principal numerical findings. I ran the inspected offline replay and reproduced the binding table, fresh-test AUCs of $0.800$, $0.701$, and $0.714$, activation-control differences, filtering gains, and sample-agreement comparisons. An additional calculation restricted supported–contradicted comparisons to claims from the same source problem; the pair-weighted AUCs remained $0.840$, $0.729$, and $0.688$. Thus the aggregate discrimination is not merely an artifact of comparing easy problems with hard ones. These checks recompute statistics from retained outputs; they do not reproduce model inference or independently validate every checker label.
The paper is organized around a comprehensible scientific argument. It explains the interventions, controls, scoring rule, failed free-form abstention prediction, and filtering trade-off. Problem-clustered uncertainty estimates and the distinction between confirmatory and exploratory analyses are valuable. The informative abstract and conventional main-text structure meet the clarity requirement.
The novelty is narrower than the title might suggest, but sufficient. The published same-problem paper [4] concerns localization and dilution of numeric facts, not claim verification or entity-conditioned abstention. The external literature already contains the underlying ideas: P(True) self-evaluation [5]; constrained confidence-label scoring under activation injection in Torrielli et al. [7], especially §§3.3, 5.5 and Appendix O of arXiv:2605.26045v3; and useful yes/no logit margins and consensus filtering in Bauer et al. [8], Appendix A.1 of arXiv:2606.02609v2. The present contribution is the evaluation of extracted claims from open-ended reasoning descriptions, with activation controls and a binding diagnostic. It should not be presented as the first discovery that AO logits contain confidence information absent from generated answers. The references here retain the manuscript’s numbering.
The following qualifications and improvements would make the accepted contribution more precise:
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Interpret the verification result as agreement with trace-based evidence. The checker sees the problem, trace tail, and continuation. Its labels do not independently establish what information is represented in the injected vectors or used causally by the target model. No-activation and other-problem controls establish dependence on the corresponding activations, but do not distinguish reconstruction of nearby text from access to hidden computation. Likewise, stratifying by one no-activation score does not literally “rule out claim plausibility.” Narrow that statement to the tested control. A same-problem activation swap would be a useful future test of state specificity.
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Credit the closest confidence method explicitly. Section 2 mentions five methods in [7] but omits its particularly relevant positive result for constrained-label scoring. Explain how binary verification of extracted claims extends that method’s setting. Also acknowledge [8]’s yes/no-margin result. This is an attribution and scope clarification; the present claim-level evaluation remains distinct.
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Keep the baseline claim specific. The agreement baseline is lexical overlap with eight samples, not semantic entailment or a reproduction of every SelfCheckGPT variant. Its tokenization excludes one- and two-character words, including short numbers, and cannot reliably distinguish negation or role swaps. The supported conclusion is superiority to this particular baseline for two readers. The “one forward pass per claim” statement describes verification after extraction; end-to-end deployment also requires claim extraction and activation preparation. Separate those costs from judging costs.
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Make the precision–coverage trade-off concrete. At the reported threshold, the original reader retains 177 of 290 supported claims and 18 of 99 contradicted claims; GRPO retains 173 of 294 and 31 of 114; the three-layer reader retains 251 of 415 and 65 of 216. This is useful filtering, but discards roughly 39–41% of supported detail. Report supported-claim retention alongside precision. The test-set median implements a batch coverage rule, not a development-frozen threshold for online use. Unresolved claims should remain separately visible.
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Preserve the causal qualification in the binding interpretation. Only the other-sentence-first condition guarantees that the selected vectors cannot attend to the queried person. When that sentence comes second, abstention is not by itself evidence of successful absence detection. The paper already identifies this distinction; carry it into the introduction and discussion instead of broadly saying the instruction “fixes” binding. The remaining 14.5% binding error for the three-layer reader and GRPO’s substantial over-abstention matter.
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Improve the reproducibility boundary and label audit. The central fresh-test records are inspectable, but the package does not contain all dependencies and evidence claimed in §7: generation scripts reference missing
pairs_v2and original workspace files, and the development and small-model trace/annotation evidence is incomplete. Document the mapping from packagedtraces_freshrecords to original inputs, supply the missing dependencies and secondary evidence, and distinguish replay from regeneration. The small-model result consequently provides weaker corroboration than the main experiment. Checker disagreement deserves a systematic audit: for example, the three-layer claim about inverse operations to isolate $x$ on trajectory 75 is labelled contradicted despite an explicitly algebraic trace. These examples limit interpretation of absolute precision, although they do not invalidate the demonstrated ranking against the disclosed labels. Finally, describe the 40 problems as fresh for this verification evaluation: the supplied registration records their earlier use in the locator study, so “never used in development” is too broad.
Acceptance rests on the supported claim-ranking and binding results, not on calibrated probabilities, a general superiority claim over confidence methods, or proof of faithful access to internal computation. The disclosed limitations leave a meaningful, reproducible central result.