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Paper summary
This paper studies whether a single fixed activation direction can shift the same outcome-preference readout in opposite directions depending on an accurate or distorted epistemic premise. A factorial interaction over premise accuracy and consequence valence constructs the direction. The direction and intervention layer are selected on discovery domains and frozen before evaluation on 24 novel domains. Validation combines teacher-forced likelihood contrasts, free-generation judgments, random-direction comparisons, and changes to the stated causal relation. Llama-3.1-8B supports held-out two-branch writability; Qwen3-8B-Base transfers the aggregate effect but fails the finite-dose distortion-branch test. In Llama, generation yields a different branch ordering from the controlled readout, while mechanism reversal does not jointly reverse steering. The contribution is an operational demonstration of conditional steering and its limits; the paper does not establish a unique relational representation or reliable causal-rule recomputation.
Critical strengths
S1. A controlled intervention with credible held-out evidence. The factorial construction cancels the designed additive main effects, and the use of shared clauses makes the comparison more controlled than independently written positive and negative prompts (Eq. (1), p. 3; Table 3, p. 14). More importantly, both branches use the same favorable-minus-unfavorable readout and must change in opposite directions. This criterion distinguishes the claimed interaction from a generic valence shift. Discovery-only layer selection and the frozen intervention provide a meaningful separation between construction and evaluation (Appendix C.1, p. 21). On the 24 novel Llama domains, the branch-oriented slopes are S_A = 0.587 and S_D = 1.073, with a positive aggregate effect in all 24 domains (Table 1, pp. 4–5). Domain-level inference avoids treating seeds or checkpoints as independent replications. These results are the main reason I support acceptance: they establish the central fixed-intervention existence claim without requiring a complete mechanistic interpretation. S2. Falsification tests establish useful limits on interpreting steering. The best-of-1,024 Gaussian comparison selects a direction and orientation on discovery data, then evaluates the frozen winner on novel domains. A nearly orthogonal winner also passes the sign criterion, while the factorial direction retains a local worst-branch advantage of 0.349, with a conditional selection-aware interval of [0.134, 0.676] (Tables 2 and 11, pp. 4 and 30). The authors consequently distinguish intervention efficacy from directional uniqueness. The relation-reversal and generation analyses similarly constrain stronger interpretations: changing an explicit mechanism does not reliably reverse the intervention, and controlled likelihood changes do not guarantee the same ordering or persistence in generation. Rescoring by a second automated judge and the human calibration make the measurement limitations visible (Appendix D). These findings give the study value beyond a favorable steering result by showing which behavioral and representational conclusions that result can support.
Critical weaknesses
W1. The behavioral conclusions depend on comparisons that change dose and measurement. The controlled result uses slopes over intervention strengths from −1 to 1, whereas generation uses endpoints at ±1.5 (Eq. (3), p. 3; Table 7, p. 25). The outcome also changes from likelihoods of two specified consequences to a five-level judgment of unrestricted text. Thus the reversal in branch ordering does not isolate the transition from teacher forcing to generation. The local derivative analysis supports the controlled ordering, but does not supply a comparison at the generation dose; the discovery-domain token-normalization analysis also does not establish the novel-domain ordering under that alternative score. Persistence is additionally sensitive to the measurement instrument. On the identical calibration subset, distortion attenuation is −0.271 for the human rater and +0.042/+0.104 for the automated judges (Table 9, p. 28). The authors appropriately acknowledge imprecision in the small human sample. Together, these issues limit how strongly the behavioral inversion and persistence can be interpreted. They prevent a stronger recommendation, although they do not invalidate the held-out controlled intervention result. W2. The intervention is better established than its relational semantic specificity. The factorial contrast removes additive main effects but retains interactions correlated with semantic congruence, expectedness, or discourse coherence. The noncausal comparison reuses clauses, yet changing their linkage also changes how appropriate the consequences are. It therefore does not cleanly distinguish an epistemic–outcome interaction from a broader congruence signal. The manuscript acknowledges the missing unrelated congruence comparison (Appendix E.4, p. 35). Moreover, the relation-control statistics come from discovery domains after default-condition layer selection, rather than providing another independent held-out test (Table 12, p. 31). This matters to significance and interpretation: the evidence supports a reproducible intervention more strongly than a specifically relational representation. The nearly orthogonal Gaussian direction further demonstrates that the branchwise sign criterion does not uniquely identify the factorial direction, although this result does not itself establish a semantic-congruence explanation. The factorial direction's stronger held-out response remains an informative positive finding. I regard this as a material limit on the explanatory claim, not a requirement that the authors prove directional uniqueness. The narrower existence result and the explicit analysis of its limits remain sufficient for weak acceptance.
Questions for authors
Q1. Focused validation — compare the controlled readout at the generation dose. Does Llama's novel-domain distortion-over-alignment ordering persist for teacher-forced contrasts at ±1.5? A comparison at the generation dose, with mean-token scoring as a length-weighting check, would clarify whether the behavioral inversion survives these direct alternatives. This would affect how strongly I interpret the controlled-versus-generated comparison in W1. Q2. Clarification — explain the disagreement about persistence. What explains the opposite human and automated attenuation directions on the identical subset in Table 9? Please specify the early/late checkpoint sets and weights, and explain whether the existing scoring protocol or disagreement cases account for the difference. This would affect my confidence in the persistence interpretation, beyond the better-supported average behavioral direction. Q3. Clarification — identify the domains used to select the behavioral dose. Appendix D.1 states that the final generation seeds differ from the pilot seeds, but does not specify the pilot domains. Which domains and scores were used to choose |α| = 1.5? If they include the final novel domains, please distinguish confirmation with new seeds from generalization to domains unused for dose selection. This would clarify the independence of the behavioral evidence, without changing the separate freezing of the axis and layer. Q4. Focused validation — distinguish relational structure from general congruence. Would one unrelated congruent/incongruent control direction reproduce the branch pattern under the existing evaluation? Selecting it on discovery data and freezing it for novel domains would address the alternative interpretation in W2. The result would affect the semantic specificity I attribute to the contribution; establishing uniqueness among all directions is unnecessary.
3 comments
Response to Reviewer roQX (2/2)
Q3 — Behavioral-dose selection and independence. Thank you; this question led to a correction. Several passages of the submitted version (§4, §7, Appendices C.2, C.4 and D.1, Tables 5–7, and the reproducibility statement) incorrectly described a separate Llama dose-selection pilot. In fact, |α| = 1.5 came from an exploratory Qwen 10-seed pilot on the same 24 novel-domain contexts (IV01–IV24) (seeds 520000–520009), comparing 0.5, 1.0 and 1.5 with the weakest-branch criterion min(Q_A, Q_D). There was no Llama dose-selection pilot. The Llama manifest fixed 1.5 and the final seeds 520010–520039 before any Llama outcome was inspected (an author-recorded chronology; Appendix C.9). The Llama direction and layer were selected on discovery domains only and the behavioral seeds were new, but the dose was not selected on domain-disjoint evidence. To answer directly: the dose-selection domains were the final novel domains, evaluated on a different model. The behavioral evidence is therefore new-seed evaluation at a cross-model, pilot-selected dose, not new-domain validation of dose selection. All affected passages have been corrected.
Q4 — Unrelated congruence alternative. We agree that the interaction contrast cancels designed additive effects without excluding generic valence matching, expectedness, or discourse coherence. For a reviewer-requested control, we prepared 48 epistemically irrelevant positive/negative premises in the 24 discovery domains (same contexts, connectors and outcome clauses) and 48 more in 24 disjoint manipulation-check domains. Two non-target automated judges from different providers (GPT-5.6 Sol and Gemini-3.6 Flash) each rated 144 items, 96 control premises plus 48 original epistemic premises as references, for 288 single-item evaluations under criteria fixed before the ratings. Only 86/96 controls passed, against a required 96/96.
The reference-item ratings also revealed an affective contrast. Both judges rated every original "accurate" premise mildly positive (+1) and the "distorted" premises more negatively (GPT: −2 for all 24; Gemini: −2 for 11, −1 for 13), so the original epistemic contrast carries a substantial affective contrast that the factorial construction does not isolate. These ratings describe the stimuli, not what the direction encodes inside Llama. The proposed controls had weaker valence contrasts (GPT 2.21 vs. 3.00, paired difference −0.79 [−0.96, −0.63]; Gemini 1.88 vs. 2.46, −0.58 [−0.83, −0.33]) and much less natural narratives (about 1.6–2.0 vs. 3.3–3.5 on a five-point scale; descriptive contrasts in Table 21).
Our pre-fixed rule blocks a control direction when screening fails. We chose not to issue a revised set during the discussion period: even strongly worded outcome-irrelevant premises (e.g., hideous, repellent) were rated only mildly negative by both judges (Table 20 includes one such example), so a revision within this design would likely remain a weaker valence manipulation, and our prewritten interpretation rule treats a null result from a weaker-valence control as weak evidence. These are limitations of the proposed stimulus design, not evidence that all unrelated-valence controls would be ineffective. No control direction was constructed or evaluated, and no target-model inference used the control stimuli. Appendix I reports this as an unsuccessful feasibility audit, and §7 retains generic congruence as an unresolved alternative.
Accordingly, the central claim remains narrow: one frozen direction produces opposite signed changes in the same teacher-forced outcome-preference margin across premise conditions in held-out Llama domains. It does not identify a unique or specifically epistemic–causal internal direction, and the relation-control results do not establish causal-rule recomputation.
Thank you for the detailed responses. I have no further questions at this stage.
Response to Reviewer roQX (1/2)
We thank the reviewer for distinguishing the well-supported fixed-direction intervention result from stronger interpretations of semantic specificity and behavioral persistence. The revised manuscript addresses Q1–Q4 in §4, §7 and Appendices D, H and I; Q3 also led to a correction (Appendices C.2, C.4 and D.1; see the General response).
Q1 — Matched-dose teacher-forced readout. We conducted a post-review evaluation on the same 24 held-out Llama domains with the frozen block-13 direction, the original candidate consequences, and the prompt-only RMS-scaled intervention. Before evaluating the generation-matched dose, we replayed the original five-dose grid and reproduced the submitted summary statistics exactly (absolute difference 0.0; identical medians, sign counts, and bootstrap intervals). At α = ±1.5, oriented endpoint secants under total candidate log-likelihood are T_A = 0.568 and T_D = 1.008, so G = T_A − T_D = −0.440 (95% domain-bootstrap CI [−0.829, −0.048]; two-sided exact sign-flip p = 0.042). The distortion-over-alignment ordering thus persists at the generation dose under this controlled score. Length-normalized mean-token scoring provides weaker evidence: on the original grid G = −0.027 (bootstrap CI [−0.052, −0.001], but two-sided exact p = 0.061); at ±1.5 G = −0.023 (CI [−0.048, 0.002], p = 0.094). The bootstrap interval and exact test differ at the original-grid boundary, and the generation-dose comparison is inconclusive under mean-token scoring (Table 19). The original prefill-only generation audit instead yields a larger rated accurate-side trajectory effect (Q_traj,A = 0.201, Q_traj,D = 0.050; B_traj = 0.151, CI [0.039, 0.279], one-sided p = 0.0094). Dose mismatch alone therefore does not account for the ordering under total likelihood, but score normalization, specified candidates versus sampled text, and judge calibration still differ. We do not claim a mechanism (§4; Appendix H).
Q2 — Human versus automated attenuation. Checkpoints are u ∈ {0.2, 0.4, 0.6, 0.8, 1.0}, with Q_early = [Δ(0.2) + Δ(0.4)]/2, Q_late = [Δ(0.8) + Δ(1.0)]/2, and C_atten = Q_early − Q_late. The middle checkpoint is excluded, weights are equal, and the late window includes the terminal checkpoint, so C_atten and Q_terminal are not independent. On the identical 480-item subset, distortion attenuation is −0.271 (human, 95% CI [−0.646, 0.125]), +0.042 (GPT-5.6 Sol, [−0.167, 0.250]) and +0.104 (Gemini-3.6 Flash, [−0.104, 0.313]); all three intervals include zero, so the subset cannot resolve the direction of attenuation. Neutral-score rates are 30.6%, 62.9% and 70.4%. Removing the terminal checkpoint from the late window moves the human estimate to −0.021, locating much of the difference in terminal judgments without explaining it. The human sample has one external rater and one matched seed per domain and branch, and the terminal checkpoint often reflects the 192-token cap rather than a natural ending. We now describe fine temporal attenuation as instrument-sensitive and secondary to the more robust trajectory-average direction (§4; Appendix D.7).