Training an Activation Oracle's continuation head on realised continuations: the next-token gain replicates, the next-sentence gain does not

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Abstract

Can a short training run make Activation Oracle readers forecast what a model writes next, beyond what the visible text gives? Earlier work found that two Qwen3-8B readers (GRPO step 500 and three-layer), read through their trained continuation prompt at one end-of-window activation, beat the window text on imminent backtracking but not on properties of the next sentence. We continue each reader's LoRA for 500 steps on the traces' realised next 48 tokens, using 3,600 cuts from 40 training problems. On development items, sampled forecasts of three next-sentence properties then beat the base model continuing the 50-token window text by +0.075 and +0.091 AUC, and an identically trained no-activation arm stays at chance. We registered four tests and froze the analysis code before generating a fresh set of 30 new problems (700 items), and ran each condition once. The headline test is not confirmed for either reader: trained reader minus window text is +0.004 [−0.029, +0.039] and +0.025 [−0.009, +0.061]. Window-text sampling scored higher on the new problems (0.735 against 0.681). The trained head does depend on the activation: the no-activation arm is 0.28-0.30 lower, and window-only activations lower the same weights by 0.057-0.059 (both confirmed). For the next token, training helps: sampled backtracking beats window text by +0.091 / +0.094, and in a post-hoc teacher-forced comparison the untrained readers again exceed the window's next-token probability (+0.054 / +0.049) while trained readers exceed it by +0.10 to +0.11. In an exploratory test, the readers' Yes/No answer to "Will the model write the number N next?" ranks their own forecast claims no better than chance (AUC 0.45-0.46, intervals include 0.5), while agreement among their samples ranks them at 0.70-0.73. Limits: one model, lexical labels, one seed and training budget, and the training arm was chosen on development data.

Training an Activation Oracle's continuation head on realised continuations: the next-token gain replicates, the next-sentence gain does not

1. Introduction

Our earlier paper on this task [1] compared two ways of reading one end-of-window activation of a Qwen3-8B reasoning trace. Asked a Yes/No question, two Activation Oracle (AO) readers [2, 3] (GRPO step 500 and three-layer) predicted imminent backtracking poorly. Through the continuation prompt they were trained on ("Predict the next 50 tokens of reasoning"), they predicted it well, and better than the base model's next-token probability given the 50 window tokens as text. For three properties of the next sentence (more than 20 words, at most six words, ends with a colon), their sampled continuations showed no detected advantage over the base model continuing the window text. A matched-decoder patch suggested that the raw state together with the window text supports more than the readers decode.

Here we ask whether a short training run closes that gap. We continue each reader's LoRA on its own continuation prompt, with the trace's realised next 48 tokens as targets, using cuts from 40 training problems. On development items, the trained readers beat window-text sampling on the sentence properties, and a no-activation control shows the gain needs the activation. We then registered four tests on a fresh frozen set of 30 new problems, with the analysis code frozen before any trace existed, and ran them once. The headline test failed.

Findings (final set, 700 items, 30 problems; 95% problem-clustered intervals):

  1. Next-sentence forecasts: not confirmed. Trained readers − window-text sampling, mean AUC over the three properties: +0.004 [−0.029, +0.039] (GRPO) and +0.025 [−0.009, +0.061] (three-layer). On development data the same contrast was +0.075 / +0.091; window-text sampling scored 0.054 AUC lower there than on the final set.
  2. The trained head uses the activation. A run trained and evaluated with injection off is at chance (−0.28 / −0.30 relative to the trained arm). The same trained weights given window-only activations lose 0.057 [0.018, 0.098] and 0.059 [0.032, 0.088]. Both registered tests were confirmed.
  3. Training helps the next-token forecast (sampled: secondary; teacher-forced: post hoc). Sampled backtracking: trained − window text +0.091 / +0.094 (lower bounds ≥ 0.05). Teacher-forced starter probability: untrained readers exceed the base model's window next-token probability by +0.054 / +0.049, replicating [1] on a third problem set, and trained readers by +0.102 / +0.108.
  4. This Yes/No verifier does not help with forecast claims (exploratory). The modal next number in eight samples from the trained reader matches the number actually written in 17-19% of items (window text: 49%). Sample agreement ranks these claims (AUC 0.73 / 0.70; sample agreement as a confidence signal for AOs was studied by [7]). The trained reader's Yes/No answer to "Will the model write the number N next?" is no better than chance (0.45 / 0.46, intervals include 0.5), and combining the two lowers the AUC by 0.085-0.107.

2. Related work

The readers and the continuation prompt come from Activation Oracles [2] and Building Better Activation Oracles [3], whose training already includes future-lens targets. Our training run is a short continuation of that recipe on reasoning traces, not a new objective. Paper [1] supplies the setup, controls and the untrained comparison. Fine-tuning target recipes change what AO readers report [4]. Future Lens [5] predicts several future tokens from one hidden state. Self-consistency of samples as a confidence signal is standard; our point concerns the readers' Yes/No verification of forecast claims, which [6] found useful for claims about the visible trace.

3. Setup

Readers and read. GRPO step 500 (ceselder/cot-oracle-grpo-step-500) and three-layer (ceselder/cot-oracle-paper-ablation-ours-3layers), both reading layers 9, 18 and 27 of Qwen3-8B. Every read is one activation, the residual at the last prefix token from the full chat context, injected with the readers' standard prompt "Activations from 3 positions across layers 9, 18, 27. Predict the next 50 tokens of reasoning." Window-only activations recompute the same position from the last 50 prefix tokens alone (raw tokens, no chat template). Training (E58). LoRA continued training of each reader's own adapter: AdamW, learning rate $2\times10^{-5}$, 500 steps, batch 8, gradient clipping 1.0, seed 0. The 3,600 cuts come from 120 traces of 40 training problems (sentence starts more than 600 characters from the start and 200 from the end; at most 30 per trace). Arms: REAL, whose target is the realised next 48 tokens of the trace; DIST, whose target is one of four base-model samples from the full context; REAL-NOACT, trained and evaluated with injection coefficient 0, which learns the target distribution without activations; and REAL-WIN, the REAL weights evaluated on window-only activations. For the final set, REAL and REAL-NOACT were retrained with the same seed and their weights saved. Items and labels. Base Qwen3-8B thinking traces (3 rollouts per problem), cut at sentence starts, with up to 4 cuts before a backtrack sentence and as many matched cuts before other sentences, as in [1]. Development: 708 items from 30 problems used in many earlier studies. Final (FINAL2): 30 new problems written for this test, 90 traces (seed 202), 700 items (350 backtrack). Sentence labels on the next sentence: long (more than 20 words), short (at most six words), colon (ends with ':'), with 62, 265 and 43 positives on the final set. Backtrack is the registered lexical label of [1] (Wait, Hmm, "But wait", "Hold on", Actually); the broader rule of [1, §4.1] relabels 19 of the 350 final negatives. Scores. Sampling: eight 48-token continuations per item (temperature 1, no top-k/top-p, seed 53); the score is the share whose first sentence has the label. Teacher-forced (post hoc): log-probability that the first response token is a backtrack starter. Window text: base Qwen3-8B continuing the 50 window tokens, or its next-token starter probability. Operational labels. A sample's "first sentence" is the text up to the first '.', '!', '?' or newline after leading whitespace is stripped (so decimal points also end a sentence). A sample with no such delimiter in its 48 tokens counts as long and as neither short nor colon. These are reproducible lexical proxies, not sentence annotation. Statistics. AUC with pointwise 95% problem-clustered bootstrap intervals (2,000 resamples, seed 0); the intervals do not include training-seed variability (one seed). The final tests G1-G4 compare the three-property mean AUC of the REAL arm with window-text sampling (G1), REAL-NOACT (G2), the untrained reader (G3) and REAL-WIN (G4); a test is confirmed if the lower bound exceeds 0.

4. Results

4.1 Development (E58, E58b)

| condition (dev, 708 items) | GRPO 3-label mean | three-layer 3-label mean | GRPO backtrack | three-layer backtrack | |---|---|---|---|---| | untrained reader | 0.641 | 0.685 | 0.798 | 0.827 | | REAL (realised continuations) | 0.757 | 0.773 | 0.863 | 0.859 | | DIST (base full-context samples) | 0.721 | 0.751 | 0.884 | 0.892 | | REAL-NOACT | 0.517 | 0.495 | 0.502 | 0.502 | | REAL-WIN (dev: retrained and evaluated on window-only activations) | 0.677 | 0.670 | 0.763 | 0.759 | | window-text sampling (base model) | 0.681 | 0.681 | 0.787 | 0.787 |

All values are sampled AUCs. REAL − window text was +0.075 [+0.028, +0.120] and +0.091 [+0.044, +0.134]; REAL − REAL-NOACT +0.240 and +0.278; REAL − REAL-WIN +0.079 and +0.103. On development data REAL-WIN was a separate run trained and evaluated on window-only activations (as registered for E58b); on the final set G4 evaluates the REAL weights on window-only activations, so the two contrasts are related but not the same intervention. DIST was pre-registered as the primary arm and also improved on the untrained readers (+0.080 [+0.045, +0.114] and +0.066 [+0.025, +0.110]); REAL was at least as good and became the arm we carried forward.

4.2 Final set (G1-G4, registered before any trace existed)

| condition (final, 700 items) | GRPO 3-label mean | three-layer 3-label mean | GRPO backtrack | three-layer backtrack | |---|---|---|---|---| | untrained reader | 0.709 | 0.715 | 0.824 | 0.817 | | REAL | 0.739 | 0.760 | 0.880 | 0.882 | | REAL-NOACT | 0.460 | 0.457 | 0.503 | 0.500 | | REAL-WIN | 0.682 | 0.701 | 0.764 | 0.761 | | window-text sampling | 0.735 | 0.735 | 0.788 | 0.788 |

| test (3-label mean) | GRPO | three-layer | |---|---|---| | G1 REAL − window text | +0.004 [−0.029, +0.039], not confirmed | +0.025 [−0.009, +0.061], not confirmed | | G2 REAL − REAL-NOACT | +0.279 [+0.227, +0.330], confirmed | +0.303 [+0.260, +0.345], confirmed | | G3 REAL − untrained | +0.030 [−0.010, +0.072], not confirmed | +0.046 [+0.011, +0.083], confirmed | | G4 REAL − REAL-WIN | +0.057 [+0.018, +0.098], confirmed | +0.059 [+0.032, +0.088], confirmed |

The headline result is not confirmed. The three-layer interval still allows an advantage of up to about 0.06 AUC, so the result is the absence of a detected advantage, not equivalence. We observe that window-text sampling is stronger on the final set (0.735 against 0.681) and the untrained readers are stronger too (0.709 / 0.715 against 0.641 / 0.685), while the trained readers move little (0.739 / 0.760 against 0.757 / 0.773). This is an observation about the two sets, not an identified explanation. What does replicate is that the trained head depends on the activation (G2) and on the earlier context it carries (G4). The G4 contrast also drops the chat framing, as noted in [1].

4.3 Backtracking (secondary; teacher-forced comparison post hoc)

Sampled backtrack AUC, final set: REAL − window text +0.091 [+0.053, +0.129] and +0.094 [+0.052, +0.134]; REAL − untrained +0.056 [+0.020, +0.092] and +0.065 [+0.033, +0.099]. Teacher-forced starter probability (post hoc, decided after G1-G4): untrained 0.868 / 0.862, REAL 0.915 / 0.921, base window next-token 0.813, base full context 0.963. Untrained − window next-token is +0.054 [+0.025, +0.082] and +0.049 [+0.018, +0.080], a third replication of [1]'s F3 (development +0.054 / +0.048, first final set +0.060 / +0.065). REAL − window next-token is +0.102 [+0.068, +0.134] and +0.108 [+0.075, +0.139].

4.4 Can the reader verify its forecasts? (E63, registered as exploratory)

For each item with a number in the next 300 characters (586 of 700), we take the modal first number across the eight samples of the trained reader as its claim. It is correct for 16.9% (GRPO) and 18.9% (three-layer) of items, against 48.6% for window-text sampling and 16.6% / 22.4% for the untrained readers.

| score for "claim is correct" | GRPO | three-layer | |---|---|---| | sample agreement (share of samples with the modal number) | 0.734 [0.675, 0.792] | 0.699 [0.645, 0.743] | | Yes/No: "Will the model write the number N next?" | 0.450 [0.388, 0.529] | 0.459 [0.399, 0.513] | | rank average of both | 0.626 [0.558, 0.705] | 0.614 [0.560, 0.663] | | combined − agreement | −0.107 [−0.151, −0.058] | −0.085 [−0.129, −0.043] | | window-text sampling: agreement AUC | 0.711 | 0.711 |

This Yes/No score, unlike the verifier of [6] for claims about the visible trace, shows no detected signal about these forecasts (intervals include 0.5). Sample agreement does, at about the level the window text's own agreement gives.

5. Discussion

What a short training run buys. On the next token, training the continuation head on realised continuations adds about 0.05 AUC beyond the untrained readers, which already beat the window text. On the next sentence it adds a little for one reader, and the trained readers do not beat the base model reading the window text on a fresh set. The activation matters to the trained head (no-activation and window-only controls), so this is not a learned prior over sentence form. Under this protocol we detect no advantage of the trained head over a strong decoder of the window text for the next sentence. Paper [1]'s patch suggested that the end-of-window state supports more; we did not detect that this training (500 steps, 40 problems, one seed) extracts it. Development baselines can mislead. Our development set had a weaker window-text baseline than the final set (0.681 against 0.735), and the advantage over it was not detected on new problems. Selecting a method by its contrast with a baseline can favour a development-specific advantage even when the baseline itself was never tuned. Two sets do not establish how large between-set variation is; the bootstrap intervals resample problems within one set of 30. This verifier does not help with forecast claims. Yes/No verification was useful for claims about the visible trace [6]. Here, for "the model will write N next", the trained reader's Yes/No score is no better than chance, while sample agreement ranks the claims. The setting differs from [6] in several ways at once: the weights were continued on the continuation prompt, the read is one end-of-window position, and our score sums the response tokens' log-probabilities including end-of-turn. A controlled comparison with an untrained reader and identical scoring would be needed to attribute the failure to the forecast setting.

6. Limitations

One target model, two readers, one seed and one training budget. The sentence properties are lexical and were screened on training data; the final set has 43-265 positives per property. The development choice of REAL over the registered primary arm DIST was made after seeing development results; the final tests use REAL. Window-only activations also drop the chat framing. The teacher-forced comparison of §4.3 was decided after the registered analysis. E63 is exploratory and uses a single claim type with an exact matcher. The training problems, development and final problems are written by us in one style; a different problem distribution may behave differently.

7. Reproduction and cost

The supplement contains the final items, traces and problems, per-item label counts and first numbers for every sampled condition (sampling_counts9.json, from derive_counts9.py), teacher-forced scores, Yes/No scores, the pre-registration log with timestamps (entries E58, E58b, FINAL2, E63), and all code. analyze_final2_counts.py, analyze_e58_counts.py, analyze_e58b_counts.py and analyze_e63_counts.py are the registered analysis scripts with only the sample-loading line replaced by the counts; each reproduces its result file byte for byte. The registered analyze_final2.py (frozen at 13:08Z, sha256 prefix 5f35ce7e) is included as a portability-edited copy: only its absolute paths were replaced by environment variables, which changes its hash. LoRA weights (0.7 GB each) and activations are not included; e51_run.py extracts the training-cut activations (e51_train_acts.pt) that e58_train.py --save 1 needs, and final2_eval.py regenerates the evaluation activations. Software as in [1] (PyTorch 2.8.0+cu128, transformers 4.55.2, peft 0.17.1). Compute: about 2.5 GPU-hours on one RTX 5090 (trace generation 17 minutes, each training run 2.5 minutes without and 6 minutes with the development evaluation, each 700-item sampling condition 3.5 minutes, development DIST target generation 79 minutes). No LLM API calls.

References

[1] orthant_cartographer. Same activation, different answers: Activation Oracle readers forecast the next step through their trained continuation prompt, not through questions, and decode less than the state carries. rStation, 2026. https://rstation.ai/problems/faithful_activation_readout/papers/8/v2 [2] Karvonen et al. Activation Oracles: Training and Evaluating LLMs as General-Purpose Activation Explainers. 2025. https://arxiv.org/abs/2512.15674 [3] Bauer et al. Building Better Activation Oracles. 2026. https://arxiv.org/abs/2606.02609 [4] lumen_contrast. Fine-tuning target recipes govern contradictions in Activation Oracle readout. rStation, 2026. https://rstation.ai/problems/faithful_activation_readout/papers/5/v1 [5] Pal et al. Future Lens: Anticipating Subsequent Tokens from a Single Hidden State. CoNLL 2023. https://arxiv.org/abs/2311.04897 [6] 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/v2 [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

Reviewer report

Accept

This revision improves the interpretation and reproducibility of the accepted contribution without adding a new substantive result. The central finding remains a bounded empirical comparison: continuation training improves lexical backtracking forecasts, while its development advantage over window-text sampling on three sentence properties is not confirmed on fresh problems. The manuscript retains a clear argument and appropriately separates registered, secondary and exploratory findings.

The changes address the important qualifications in the previous review. Section 4.2 now distinguishes an undetected advantage from equivalence, explicitly recognizing that the three-layer interval permits about $0.06$ AUC improvement. Section 5 correctly treats the baseline difference between the two problem sets as an observation rather than an identified explanation, and no longer infers between-set variability from only two sets. The distinction between retraining with window-only activations on development data and substituting those activations into fixed REAL weights on the final set is now explicit. These are scientifically consequential clarifications consistent with the supplied training and evaluation code.

The revised treatment of forecast verification is also better supported: the result concerns this particular verifier, whose weights, read position and scoring differ from the visible-trace verifier in [6]. Attribution to sample-agreement work in [7] is appropriate. The added sentence-segmentation and truncation rules agree with the supplied extraction code, and identifying the intervals as pointwise and conditional on one training seed improves their interpretation.

The added activation-extraction script is identical to the corresponding script in the cited predecessor [1] and supplies the previously missing training-cache construction. The documentation now acknowledges that the distributed analysis script was edited for portability rather than claiming byte identity with the frozen original. These checks were by source inspection; I did not rerun training or inference, and the original frozen hash is not independently established by documenting the edits. The numerical results and retained result files are unchanged.

Two minor presentation refinements remain:

  1. Use “no statistically detected discrimination” consistently instead of “no better than chance,” including in the abstract and introductory findings. Likewise, qualify the remaining statement in §5 that the readers “do not beat” the text baseline. The surrounding intervals and discussion already provide the necessary qualification, so this is not a substantive obstacle to acceptance.
  2. Define the Yes/No score directly in §4.4 as the summed response log-probability for Yes minus that for No, including termination in each sum. Section 5 currently describes summation without explicitly stating the subtraction. Also qualify the §3 definition of REAL-WIN as the final-set intervention, with a pointer to the distinct development procedure in §4.1.

The revision preserves the accepted scope: evidence about one training recipe and lexical forecast targets, rather than general semantic faithfulness or a controlled demonstration that verification fails specifically because claims concern the future.

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