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Under review as a conference paper at ICLR 2027

Representational Control over Self-Report & Behavior Coherence in LLM Risk-Taking

Abstract

Self-report is an appealing low-cost probe of an LLM’s dispositions, but recent work finds only selective agreement between what models report and how they behave. Prior accounts establish these patterns by prompting black-box LLMs, leaving open whether the gap is a prompting artefact or a fact about how the underlying constructs are represented internally. We investigate risk-taking, a consequential dimension of agentic decision-making, using activation steering to measure self-report and behavior under the same internal intervention. We survey nine steering-vector extraction methods spanning task-specific directives, the model’s own task behavior, and dispositional descriptions at two granularities, evaluated on two behavioral tasks and two psychometric instruments across four open-weight LLMs. We find that (1) a shared internal intervention does not ensure shared responsiveness: directions built from trait descriptions move self-report but leave behavior at chance, directions built from the model’s own task choices do the reverse, and only task-specific directives reach both, weakly. (2) Diagnosis dissolves that exception: removing surface confounders leaves the directives only 32% of their behavioral effect. The two channels are otherwise steered by near-orthogonal directions, each reached by multiple, separately constructed directions. (3) Composing a behavior-moving and a self-report-moving direction moves both channels together; flipping one sign drives them apart instead, reaching states in which what a model reports contradicts what it does on 69–89% of such blends in all four models. These findings move the self-report↔behavior relationship from a black-box observation to a representational one that can be inspected and controlled, motivating representational checks alongside behavioral evaluation.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM self-report, behavioral evaluation, self-report behavior dissociation, model auditing, interpretability, risk-taking, psychometrics, activation steering

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_iKv9OpenReview ↗
Rating
3(+1)
Confidence
2(−1)
Informativeness
2
Presentation
3
Soundness
3(+1)
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Paper summary

This paper investigates the relationship between self-reported risk preferences and risk-taking behavior in LLMs through activation steering. The authors compare nine steering-vector extraction methods across four open-weight LLMs, two behavioral tasks (CCT and BART), and two self-report instruments (BFI and DOSPERT).

The experiments are organized around three research questions. First, the authors find that vectors derived from behavioral choices primarily affect behavior, while trait-based vectors mainly affect self-reports. Second, geometric and ablation analyses suggest that these directions are largely separable, and that the behavioral effects of task-specific instruction vectors are substantially driven by surface-level cues. Third, combining behavioral and self-report steering vectors can induce either aligned or opposing changes in the two outcomes.

The authors argue that these findings provide a representational perspective on self-report–behavior dissociation and motivate mechanistically informed behavioral auditing.

Critical strengths
  • Systematic experimental evaluation. The paper compares nine steering-vector extraction methods across four LLMs, two behavioral tasks, and two self-report instruments. This provides a relatively comprehensive comparison of how different supervision sources affect the two outcomes.

  • Careful controls and robustness analyses. The authors include random-direction baselines, dose variations, lexical shortcut controls, and projection-based ablations. These analyses help distinguish the effects of different steering methods and address several potential confounders.

  • Going beyond behavioral observations. Rather than simply documenting self-report–behavior dissociation, the paper examines the geometric relationships and functional dependencies among steering directions, providing additional evidence about their internal organization.

  • Clear experimental structure. The three research questions follow a coherent progression, from identifying selective steering effects to analyzing their representational relationships and testing compositional control. The presentation is generally clear and well organized.

Critical weaknesses
  • The behavioral measures do not adequately distinguish risk preference from other decision variables. The paper defines risk-taking using the probability of choosing more than half of the maximum number of cards or pumps. However, this numerical midpoint has no clear decision-theoretic justification. In CCT, the risk-neutral optimal choice depends on the payoff and loss probabilities, while in BART, the explosion threshold distribution is unknown to the model. Moreover, the behavior-derived steering vectors are extracted by contrasting high-choice and low-choice conditions, which may capture task features or choice magnitude rather than risk preference. Although the authors examine lexical shortcuts, their controls do not fully rule out numerical response biases. Evaluating the same vectors on non-risk numerical tasks and binary risky choices would help distinguish these explanations.

  • The representational interpretation is stronger than the evidence supports. The authors show that steering vectors derived from different supervision sources have largely separate effects and are nearly orthogonal. However, behavior-derived vectors and trait-description-derived vectors may naturally capture different computational variables. Their geometric separation does not necessarily imply that the underlying risk-related representations governing self-report and behavior are distinct. In particular, the experiments do not establish whether these vectors capture a shared latent risk preference in the first place.

  • The operationalization of self-report–behavior coherence is not fully aligned with the motivating question. The paper motivates its investigation by asking whether self-reports reflect or predict actual behavior. However, coherence in RQ3 is defined by whether steering produces changes in the same direction across the two readouts. Such directional agreement does not establish predictive consistency between self-report and behavior. Consequently, the connection between the demonstrated compositional control and the original self-report–behavior consistency problem remains unclear.

  • Limited behavioral generalization and validation of steering effects. The authors' own results show that behavior-derived steering vectors retain only approximately 7% of their effects when transferred between CCT and BART, raising concerns about whether they control a general risk-taking tendency. In addition, behavioral outcomes are evaluated through answer-token probabilities rather than actual generated decisions. This is particularly concerning for BART, where valid numerical answers account for only about 4% of the output probability mass. The paper does not sufficiently establish whether the interventions preserve normal model functionality or produce comparable effects in naturalistic decision-making.

  • The implications for mechanistically informed behavioral auditing remain largely speculative. RQ3 demonstrates that selected behavior-moving and self-report-moving vectors can be combined to induce opposing changes in predefined readouts. However, the paper does not evaluate an actual auditing procedure or demonstrate that representational checks improve the detection or prediction of problematic behavior compared with black-box evaluations. Given the limited cross-task generalization, the practical significance of these results for behavioral auditing remains unclear.

Questions for authors

I don't have any questions.

5 comments
AuthorsOpenReview ↗

Response to Reviewer iKv9: threshold, predictive consistency, functionality, auditing

Thank you for the review. Shared points are answered in the General Response:

  • Non-risk numerical tasks and binary risky choice (W1) in S3
  • Shared latent risk preference and cross-task transfer (W2, W4) in S6
  • Answer-token probabilities vs generated decisions (W4) in S1
  • BART admissible mass (W4) in S2

Justification of the ">half the max" threshold (W1-b)

We chose this score so that behavior and self-report are measured the same way, and its midpoint is conservative in decision-theoretic terms. Every readout is the log-odds of the upper vs lower half of its response scale, read from the answer distribution (as in Santurkar et al., 2023), so channels share one rule, free of sampling noise and ceiling. For behavior, the midpoint is at or above the risk-neutral optimum: in BART, k > N/2 is at or above k* = argmax k(1−p)^k (burst probability p) on every round; in CCT, k* is at most 6 cards on 7 of 8 boards, against 16. Choosing above the midpoint is therefore risk-seeking. The score does not register a shift that stays on one side of the midpoint, so we checked it two ways.

Scoring by the mean leaves the conclusions unchanged. The mean no. of cards/pumps registers shifts anywhere on the scale and does not depend on k*, which matters for BART as the model is not told p. It gives the same verdict in 93% of the paper's behavioral cells, with the same family pattern: own-choice vectors 16/16 on each measure, task-instruction vectors 11/16 on each, dispositional vectors 0 and 2 of 40, the two extra cells marginal and gone on the format-constrained BART prompt (App. C.5.8; S2).

Generated decisions agree as well. Sampled choices, with no threshold, track the log-odds score at r = 0.91–0.98 within each model and confirm that dispositional vectors leave behavior unmoved (16 of 16 cells; S1).

Directional coherence vs predictive consistency (W3)

RQ3 tests predictive consistency in the form an audit relies on: whether a change in self-report predicts a change in behavior. Prior black-box work tests the cross-sectional form: across models or conditions, does what a model reports predict what it does. An audit faces the interventional form whenever a model changes, through retraining or a new prompt, and reads a shift in its reported disposition as evidence of a shift in its behavior. RQ3 tests that inference and shows it can fail: composition drives the two channels apart in 77.4% of anti-aligned compositions. App. E.3 now states this relation; thank you.

Preserved functionality (W4-b)

At the paper's dose, steering leaves general capability intact (Tab. R4). We added the 3 capability checks from the steering work: MMLU accuracy, perplexity and next-token KL from the unsteered model, on tinyMMLU (100 items) and 200 WikiText-103 passages, for all vectors and random directions in all models (App. C.5.13). Accuracy changes by −2 to +5 pts, within tinyMMLU's standard error (~5 pts), and no cell falls outside matched random directions (0 of 104). Perplexity changes by a median of +0.2% to +2% per family (max 4.7%), and KL max 0.07 nats/token.

Table R4. Change from the unsteered model at α = ±1: median [min, max] over cells; damage = cells outside size-matched random directions; OLMo's two own-choice vectors at α = ±0.25/±0.5, matched relative size (App. C.5.13).

FamilytinyMMLU (points)Accuracy damagePerplexity (%)KL (nats/token)
Task instructions (a)0 [−2, +4]0/32+0.4 [−0.9, +2.4]0.007 [0.002, 0.020]
Own choices (b)+1 [0, +2]0/32+0.2 [−1.5, +3.4]0.004 [0.001, 0.061]
Risk dispositions (c)+1 [−1, +5]0/24+2.0 [−0.7, +4.7]0.025 [0.014, 0.070]
Big-Five profiles (d)+1 [−1, +3]0/16+1.2 [−0.3, +4.6]0.013 [0.006, 0.069]
Random directions0 [−1, +2]1/640.0 [−0.4, +0.4]0.001 [0.000, 0.003]

The 64 RQ3 compositions behave the same (0 of 128 accuracy cells damaged; App. C.5.13).

Capability declines only above the doses we interpret. Through α = 4, the median change in tinyMMLU accuracy per family is 0 to +3.5 points; losses become common only at α = 8, where App. C.5.4 already finds effects flattening; every conclusion rests on lower doses.

Auditing implications (W5)

Our results show that black-box coherence can mislead audit and provide cheap check Self-report and behavior can agree without a shared mechanism: task-instruction vectors move both, but their behavioral side rests largely on a quantity-instruction component (32% retained; RQ2), and the two channels can be driven apart (RQ3). Observed agreement therefore does not guarantee a shared disposition. Geometry flags this before any behavioral run: directions moving the same channel are more aligned than those moving different channels (by 0.41 in mean |cos|, significant in every model; RQ2). Benchmarking such checks is future work, which we added to the limitations.

Thanks to the authors for the detailed rebuttal and additional experiments. The generated-choice validation and functionality checks address several of my technical concerns.

However, my main concern about the representational interpretation remains. The behavior-derived vectors show strong task dependence (~7% cross-task transfer), affect non-risk numerical choices (10/16), and generalize weakly to independent risky choices (2–4/16). These findings seem more consistent with task-specific choice representations than a shared risk-preference representation.

If the vectors barely generalize across behavioral risk-taking tasks, their separation from self-report vectors does not necessarily establish a specific self-report–behavior representational dissociation. The broader auditing implications also remain largely untested. I therefore maintain my score.

AuthorsOpenReview ↗

Clarifying transfer: low retention reflects large native effects, not missing cross-task behavior

Thank you for the follow-up. We believe there is a miscommunication about what the transfer numbers show, and we apologize for not making it clearer.

Low retention does not mean behavior vectors fail to move behavior on other tasks.

Retention is a ratio: the effect on the other task divided by the effect on the vector's own task. Own-choice vectors steer their own task very strongly (median 44.8 control SDs), so a carried-over effect of 3.1 is only 7%. Task-instruction vectors, built by a completely separate method, have a much weaker native effect (6.6), so a similar carried-over effect of 5.0 is 76%. In absolute terms, both families move behavior on tasks they were not built on, at comparable rates and effect sizes:

Table R5. Cells clearing the random-direction control (z ≥ 3.5), and median z over all cells, cleared or not (retention relative to the own task), at the paper's dose.

FamilyOwn task: clearzOther risk task: clearz (retain)Number-free lottery: clearz (retain)
Task instructions11/166.69/165.0 (76%)5/162.2 (34%)
Own-choice16/1644.87/163.1 (7%)4/162.1 (5%)
Dispositional——0/400.4–0.70/200.9

Dispositional vectors are not built on any task, so their CCT and BART cells are all "other"; 0.4–0.7 are the medians of the risk-described and Big Five families.

The lottery has no cards, pumps or counts, so the reach of both behavior families there is not a number-size effect.

The contrast is the dispositional family.

These vectors move self-report across instruments (31/40 cells) but clear the control on none of the behavioral measures: 0/40 on CCT and BART, 0/20 on the lottery. Conversely, what generalizes on the behavior side does not reach self-report: own-choice vectors clear 0/16 BFI cells once agreement is removed.

The standard the reviewer describes is exactly the pattern we report. Vectors built from the model's own choices move behavior across tasks but not self-report, and dispositional vectors move several self-report instruments but no behavior. This is the self-report–behavior dissociation the paper claims.

RQ2 shows how the one family that reaches both channels does so.

Task instructions move both self-report and behavior, but through different components. Removing the twelve surface controls takes away about two-thirds of their behavioral effect, on their own task (32% remains, App. C.5.4) and, in a new analysis, across tasks (34% [25, 44] remains), but only about a third of their self-report effect (64% [57, 70] remains). The part that carries their behavior is largely the "choose many" component that CCT and BART share; the part that moves self-report mostly survives its removal. Even in the family that looks coherent, the two channels are moved by different parts of the vector.

We agree that whether this surface reliance counts as part of measuring general risk-taking, or as a shortcut, is a fair topic for discussion. Either way, the paper shows both the effects and the mechanism that produces them, and we will make the transfer results and Tab. R5 explicit in App. C.5.3.

Reviewer_pgyGOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper investigates the gap between what LLMs say about their risk-taking and what they do. It builds nine kinds of steering vectors and injects them into four 7-8B open-weight models. Behavior is read on two risk tasks and self-report on two questionnaires, from answer-token likelihoods. Disposition vectors move self-report but not behavior, while own-choice vectors do the reverse. They find that composing them with opposite signs makes the channels disagree in most of the cases.

Critical strengths
  • Using internal steering instead of prompting is a reasonable idea, since the same intervention is applied to both channels.
  • The design is thorough and careful. The paper also reports its own limitations honestly.
Critical weaknesses
  1. I am somewhat concerned about circularity in the behavior result. The own-choice vectors are built from the model's own high vs low choices on the same datasets used for the behavior readout, with no held-out tasks.
  2. The RQ1 logic assumes that if a shared risk representation exists, one steering vector should move both channels. A possible and simpler hypothesis is that the extracted vectors do not generalize beyond the context they are extracted in: trait vectors are extracted on neutral text and own-choice vectors at the task decision token, and each moves the readout closest to its extraction context. It's not clear to me how this hypothesis is ruled out.
  3. The only dimension tested is risk-taking. Self-report and behavior can disagree on many other dimensions, such as other personality traits or stated values. So it's not clear the conclusions of this paper can generalize.
  4. (Minor) The models are also only four 7-8B instruct models. Some evaluations on larger models could further solidify the results.
Questions for authors

See weaknesses.

3 comments
AuthorsOpenReview ↗

Response to Reviewer pgyG: circularity, scope beyond risk-taking, model size

Thank you for the review. Shared points are answered in the General Response:

  • "Simpler hypothesis": vectors do not generalize beyond their extraction context (W2) in S5, which includes the matched-context experiment
  • Whether a shared representation should move both channels (W2) in S6

Here we address the specific unique subpoints the reviewer has raised which others have not. We hope this organization is clear and helps avoid duplications.

Circularity (own-choice vectors and the behavior readout) (W1)

The own-choice effect holds on boards and tasks the vectors were never fit on, and the dissociation rests on a channel circularity cannot reach.

  • Held-out boards (new test): for the three own-choice vectors whose extraction grids leave some evaluation boards out, we recomputed the effect only on those boards, against random directions on the same boards. It clears the control in 12/12 cells on both the threshold and the mean-choice measure and keeps a median 99% of its size (range 0.83–1.17; App. C.5.9).

  • Held-out task: the same vectors also move a risk task they were never fit on, a binary lottery with no number in the answer (2–4 of 16 cells at the paper's dose, 7–8 at twice it; S3).

  • The other channel: the dissociation rests on these vectors leaving self-report at the random-direction control; with agreement bias removed, they clear it in none of 16 BFI cells. Circularity can inflate an on-task effect; it cannot produce a null on an instrument the vectors never saw.

Only risk-taking (W3)

Risk-taking is a deliberate choice: it is consequential for agentic decisions and has validated measures for both channels. Behavioral tasks and psychometric instruments for risk-taking are established in human research. The method (constructing directions from different supervision sources and testing selective reach and composition) is not specific to risk, and the limitations now name other dispositions as next tests. A second construct would need its own validated behavioral tasks, self-report instruments and theory-grounded dispositional constructions; we think it is better done properly in follow-up work than briefly here.

Only 7–8B models (W4)

7–8B instruct models are the standard testbed for activation steering, and the dissociation we study is not specific to this scale. Steering requires access to activations, and the methods we build on were developed and evaluated at this scale: contrastive activation addition on Llama 2 7B and 13B Chat (Rimsky et al., 2024), inference-time intervention on LLaMA-7B (Li et al., 2023), the reliability analysis of steering vectors on Llama-2-7B-Chat and Qwen-1.5-14B-Chat (Tan et al., 2024), persona vectors on Qwen2.5-7B-Instruct and Llama-3.1-8B-Instruct (Chen et al., 2025), and Steer2Adapt on Llama-3.1-8B, Qwen-2.5-7B and Mistral-7B (Han et al., 2026). The self-report–behavior gap itself appears across scale in black-box studies, from 1.5B models to 70B–405B open models, GPT-4o and Claude 3.7 Sonnet (Han et al., 2025), so these models are a setting where the phenomenon exists and its internals can be inspected. Our four models span four families and training pipelines, and the pattern holds in each. Extending the analysis to larger open models is a natural next step, and the limitations explain the choice of model size.

Thank you for the detailed reply and the additional experimental results!

  • My concern about circularity is mostly addressed by the new experiments.

  • I still do not fully understand how the simpler hypothesis (that the extracted vectors do not generalize beyond the context they are extracted in) is ruled out. I would appreciate a concise explanation about this.

  • I agree that risk-taking is an important disposition. However, since the full study is based on it, I am still concerned about the usefulness of the findings beyond this disposition.

Overall, I will keep my score at 2 and see how the other reviewers discuss during the reviewer discussion period.

AuthorsOpenReview ↗

Follow-up: why extraction context alone does not explain the dissociation

Thank you for the follow-up and for engaging with our reply and new analysis; we are glad the circularity concern is addressed. We provide further details and interpretation of the analysis that we hope will help clarify the remaining concerns:

Why the simpler hypothesis does not explain the dissociation

If the vectors did not generalize beyond their extraction context, that context alone would determine which channel (self-report or behavior) a method moves. This is not the case:

  1. Vectors read in the same context reach different channels. In the paper, task-instruction and own-choice vectors are both read in the task context, yet task-instruction vectors move self-report in 15/16 cells and own-choice vectors in only 5/16. Extraction context is clearly not enough; the construction matters.
  2. Reading a vector in the other channel's context does not make it move that channel. We re-extracted every family in the other context (S5). Dispositional vectors read inside the task context barely move behavior (4/24 cells), yet keep their self-report effect (21/24).

We agree, however, and the revised paper states this, that context still matters, but it is not sufficient by itself. Task-built vectors lose their behavioral reach when read in neutral context (own-choice 16 → 2/16, task instructions 13 → 1/16). To measure how much each factor contributes, we statistically decomposed the variance in which channel (self-report vs behavior) a vector prefers (Tab. S5-B): the construction × context interaction explains the most (37%), then construction (34%), model (5%), and context alone almost none (1%). This essentially quantifies how important each factor is.

In short, the right extraction context is needed, but it is not sufficient, and construction is the more important factor. Context by itself does not determine which channel a vector moves: no family gains the other channel by being read in that channel's context, though task-built vectors lose their own channel outside the task. We hope this explanation helps clarify this.

Beyond risk-taking

Risk-taking is itself a broad disposition: it shapes decisions across many agentic applications, from financial and medical choices to whether a model acts on uncertain information or asks first. The testing methodology is not tied to risk-taking either. Building vectors from different supervision sources, testing which channel each reaches, removing shared components and composing directions all apply to any disposition. What a new domain needs is its own theoretical grounding: validated behavioral tasks, self-report instruments and constructs to build the dispositional vectors from.

Reviewer_1XScOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies whether activation steering changes an LLM's reported risk preferences and its choices in risky tasks together. It compares nine extraction methods across four models, using CCT and BART for choices and BFI and DOSPERT for self reports. Vectors extracted from descriptions of dispositions mainly change questionnaire scores, while vectors extracted from the model's choices mainly change choices on the task used for extraction. The paper examines these effects through vector projections and activation ablations, including controls for quantity and questionnaire features. It then combines vectors targeting the two outputs and tests whether their relative signs produce matching or opposing changes.

Critical strengths
  1. The comparison across extraction methods is the strongest part of the paper for me. Descriptive vectors mainly change questionnaire answers, while vectors drawn from the model's choices mainly change choices on the original task. This adds to earlier observations of disagreement between self reports and behavior by showing how the two respond to internal interventions. I also found the limited transfer between behavioral tasks interesting. Even a vector extracted from behavior has a narrow reach here. These findings matter for work on trait steering, where a change on one questionnaire or task may be taken as evidence of a more general change in disposition.

  2. I appreciate how the paper follows up on this finding. The comparisons across models and tasks, dose sweeps, and random direction controls give reasonable support for the main pattern. The projection and activation ablation experiments then examine which components carry an effect and which computations it depends on. The composition experiment is particularly interesting because it tests whether the two outputs can be moved together or apart. The broad result also holds when all endpoint cells are included. These experiments offer a promising way to study when agreement between a model's reports and choices survives internal interventions, which is useful for evaluating self reports as a guide to behavior.

Critical weaknesses
  1. I am less convinced by the explanation in terms of distinct risk representations. The experiments show that the constructed directions affect the two outputs differently. Table 2 also changes the context used for extraction: choice vectors are read at task decisions, while most descriptive vectors are read over neutral snippets. The prompting comparison in C.5.5 and the projected directive results are helpful checks, but they do not directly separate the source of supervision from the extraction context. I would qualify the claim that the source determines which channel a vector reaches. The quantity controls leave a similar question. In both tasks, taking more risk is implemented by choosing a larger count. Removing a direction for choosing many cards or pumps could remove part of the intended policy. The larger loss of behavioral effect for task instructions than for vectors extracted from choices suggests that the methods depend on different components. I do not think it establishes that the removed component is an irrelevant shortcut. Section 3 already acknowledges that these cues may express part of the intended policy. That qualification should carry through to the abstract and conclusion. Selective control remains an interesting result with this narrower interpretation.

  2. I have two concerns about what the questionnaire results establish. First, Appendix A.3 says that reverse keying makes a general tendency to agree cancel in BFI. Using the item counts in Table 18 and the scoring rule in B.4, a uniform increase of δ\delta in every item's original agreement log odds increases the reported risk composite by 17δ/4517\delta/45. The cancellation is therefore incomplete. I would like to see whether the main pattern survives weighting the direct and reverse items to cancel this shift. The calculation alone does not tell us how much of the observed effect comes from agreement bias, but the claimed protection needs correcting. Second, Section 4 defines coherence through the signs of the changes. A model's questionnaire score could become less risk seeking while its choices become more risk seeking, even if both resulting scores still indicate a preference for risk. I can see evidence that the two measured responses can be pushed in opposite directions. I am missing the step that establishes the stronger claim that the model reports something that contradicts its behavior. Figure 4 and Appendix E should state exactly how each administration is scored relative to the unsteered baseline and the paired swing. Appendix B.4 also reports that admissible BART answers receive little probability mass, so a check against generated choices would help interpret this as behavior.

  3. I could follow the three research questions, but I had to go back and forth between the main text and the appendices to work out what the results count. Section 2.1 introduces answer probabilities, while Appendix B.4 gives the actual scoring rules. RQ1 compares effects with a random direction band, whereas RQ3 uses the signs of changes and excludes some endpoint cells. These differences are easy to miss when reading Figures 2 and 4. The description of the control band also differs between C.4 and E.1, although this appears not to change which endpoint cells are included. I would put the scoring rules, reference point, success criterion, and included conditions for each research question in one table in the main text. Some figure panels are also difficult to read at normal page size, particularly Figure 4C.

Questions for authors
  1. What exact behavioral and questionnaire values determine the RQ3 label for each administration? How do these relate to the paired swing definition? Please make the reference point explicit and report how the rates change if both effects must exceed the random direction band. Please also clarify which administrations are included in each analysis in Appendix E.

  2. How much of the family pattern can be attributed to the extraction context? A limited comparison using matched contexts would help assess the claim about supervision source. Alternatively, could the conclusions be restricted to the particular constructions tested here?

  3. What distinguishes the removed quantity component from a quantity related part of the intended risk policy? Which current result supports interpreting the lost effect as a shortcut?

  4. Do the BFI dissociation and composition results persist when direct and reverse items have equal total weight within each subscale?

3 comments
AuthorsOpenReview ↗

Response to Reviewer 1XSc: agreement bias, scoring table, RQ3 label, control band, Figure 4C

Thank you, especially for the careful reading of App. A.3. Shared points are answered in the General Response:

  • Absolute coherence (Q1) in S4
  • Extraction context (Q2) in S5
  • Quantity component (Q3) in S3
  • Generated decisions and BART mass (W2) in S1–S2

Values behind the RQ3 label (Q1-b)

Each administration is labeled from two half-swings, y = (steered − unsteered level, same model, task and persona) / control SD, where the control SD is that of full paired swings of random directions at α = 1. An administration is anti-coherent when y_beh and y_sr differ in sign. The paired swing in the spillover analysis is a full swing (steered(+α) − steered(−α)); the RQ3 label uses half-swings against the shared baseline, so the two arms are not exact mirrors (r = −0.89 on behavior). This definition is now in App. E.1; the inclusion rule is in Tab. 2 and below.

Agreement bias and BFI reverse-keying (Q4)

Thank you for catching this; we have corrected App. A.3 and re-scored BFI with agreement cancelled exactly. Because BFI-44's subscales are not balanced, a uniform agreement shift δ still reaches our composite at about 0.17δ. We changed the Nicholson subscale weights as little as possible so that a uniform shift cancels exactly, the subscale-level equivalent of the suggested equal-item-weight scheme. The random-direction control is recomputed with the same weights (App. C.5.7).

Table R1. BFI cells (vector × model) clearing the random-direction control at α = ±1, with the paper's weights and with agreement cancelled.

VectorsCellsClear, paper weightsClear, agreement cancelled
Dispositional (c, d)201913
· Llama, Ministral, OLMo, Qwen5 each5, 5, 4, 54, 5, 3, 1
Own-choice (b)1620
Task instructions (a)16116

With agreement cancelled, the dissociation holds in three of four models and sharpens. Dispositional vectors keep their self-report effect in Llama, Ministral and OLMo (12 of 15 cells), and own-choice vectors now clear self-report in none of 16 cells. The task-instruction effect shrinks to Ministral (4 of 4) and half of Qwen. In Qwen the dispositional effect is mostly agreement (1 of 5 cells survive): steering moves that model's self-report through acquiescence rather than trait content.

The composition result (RQ3) holds in the same three models. On BFI, anti-aligned compositions move self-report and behavior apart in 65 percentage points more administrations than aligned ones with the paper's weights, and 45 with agreement cancelled (42 → 35 under the additional band test, S4). The gap holds or grows in Ministral (70 → 96) and Llama (band test: 37 → 49), shrinks in OLMo (44 → 38), and vanishes in Qwen (78 → 2).

DOSPERT, which has no reverse-keyed items, shows the same pattern under a neutral-item control. We replaced its risk items with content-neutral activities and subtracted the neutral-item effect to isolate the part specific to risk (Tab. R2). For dispositional vectors that part clears in 10 of the 12 cells where DOSPERT clears. Task-instruction vectors' effect is mostly general agreement (neutral share 0.86), with a risk-specific remainder in Ministral and Qwen; the RQ1 paragraph is revised accordingly. Own-choice vectors' small DOSPERT effect moves neutral activities as much as risky ones (risk-specific part: 0 of 5 cells), so the dissociation is cleaner than reported.

Table R2. DOSPERT neutral-item control: median effect in control SDs (cells clearing); neutral share = neutral / DOSPERT effect (0 = risk-specific, 1 = general agreement); cells whose risk-specific part clears.

VectorsCellsDOSPERT effectNeutral shareRisk-specific part clears
Dispositional (c)125.8 (7 clear)−0.066 of 7
Dispositional (d)88.8 (5 clear)0.564 of 5
Own-choice (b)161.9 (5 clear)1.090 of 5
Task instructions (a)1633.4 (13 clear)0.869 of 13

Consolidated scoring table (W3)

Tab. 2 in Sec. 2 now gathers, for each research question, the score, reference point, units, criterion, included conditions and estimator, with pointers to the appendices; no rule or result changed.

Control band in C.4 vs E.1 (W3)

The paper uses one significance band throughout; the "±2" in E.1 is RQ3's inclusion gate, not a second band. A cell clears when its mean swing lies more than 3.5 control SDs from the random-direction mean in the intended direction (Sec. 2, App. C.4). The ±2 instead decides which cells enter RQ3's main rates: those where the composition's self-report vector moves its instrument by at least 2 control SDs; ungated rates are also reported. E.1 now says so and points to C.4; thank you for spotting this.

Clearer Figure 4C (W3)

Thank you; Figure 4C now has larger text and markers, matching panels A and B.

I thank the authors for the careful responses and the amount of new analysis. I went through the revised PDF, the general response, the summary for the AC, and the threads with the other reviewers.

Two small points to be addressed, mostly conceptual ones. One is the absolute-contradiction question that Reviewer r3sE also asked. Table 30 shows that aligned and anti-aligned compositions create new absolute contradictions at the same rate (20.8%). The main text now describes coherence relative to the unsteered model, which I agree with, but the TL;DR still says that composition can "make a model report the opposite of how it acts." Matching the TL;DR to the relative wording would avoid overstatement. The second is interpretive, and here I agree with Reviewer iKv9. Directions that separate under steering do not, by themselves, show that the underlying risk representations are separate, so I'd keep that claim carefully scoped.

Overall, the rebuttal has answered most of my questions, and the points remaining are minor wording issues. I keep my rating at 3.

AuthorsOpenReview ↗

Thank you; TL;DR wording and scope of the representational claim

Thank you for going through the revised PDF and all the threads so carefully, and for the constructive review throughout.

We agree on TL;DR. Unfortunately, the TL;DR field does not seem to be editable during the discussion (only the title, abstract and the PDF are), so we will change it at the first opportunity to the relative wording of the main text:

"In LLMs, self-report and risk-taking behavior are steered by near-orthogonal internal directions, and composing them can move the two together or drive them in opposite directions relative to the unsteered model."

Scope of the representational claim. We agree here as well and, as committed to Reviewer iKv9, we are scoping the claim to what steering establishes: the directions that move the two channels are functionally separate, which does not by itself show that the underlying risk representations are separate. We have revised the abstract's closing sentence accordingly ("to the level of internal directions that can be inspected and controlled" rather than "a representational one"; marked in red in the updated PDF), matching the Conclusion and Limitations, and will review the rest of the paper and apply the same scoping throughout.

Reviewer_r3sEOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper investigates whether LLM self-reports of risk-taking and their behavioral decisions are governed by shared internal representations. The authors compare nine activation-steering methods across four open-weight LLMs, using two behavioral tasks (CCT and BART) and two psychometric instruments (BFI-44 and DOSPERT).

The results show that trait-based steering primarily changes self-reports, whereas directions derived from the models' own task choices predominantly affect behavior. Task-specific directives influence both channels, but their behavioral effects substantially diminish after removing surface-related components. Further geometric and ablation analyses suggest that the two channels are influenced by largely distinct steering directions. Finally, vector composition can induce either aligned or opposing changes in self-report and behavior.

Critical strengths
  1. A novel representational perspective on self-report–behavior dissociation.

The paper moves beyond black-box comparisons by applying activation steering to both self-report and behavioral outcomes. This provides stronger intervention-based evidence for the dissociation and helps clarify why manipulating a model's stated disposition does not necessarily change its decisions. The distinction is important for evaluating the reliability of self-report-based model auditing.

  1. Comprehensive experimental validation and diagnostic controls.

The evaluation covers multiple models, steering-vector constructions, behavioral tasks, and self-report instruments. The combination of geometric analysis, lexical controls, projection-based interventions, dose robustness checks, and vector composition provides complementary evidence. In particular, distinguishing geometric overlap from downstream computational dependence is a valuable methodological contribution.

Critical weaknesses
  1. The operationalization of risk-taking and coherence limits the interpretation of the findings.

Behavioral risk-taking is measured through log-odds over predefined numeric answers rather than actual generated decisions. This is particularly concerning for BART, where the paper reports that admissible answers account for only approximately 4% of the output probability mass. Consequently, the reported effects may not fully reflect how models would behave under ordinary generation.

Moreover, RQ3 primarily defines coherence through the signs of steering-induced changes. Opposite movements in two scores do not necessarily establish that a model's absolute self-reported risk preference contradicts its actual decisions. This distinction matters for the paper's central claims about inducing anti-coherent states.

  1. The evidence does not fully establish separation between underlying risk representations.

The near-orthogonality of the extracted steering directions is compelling, but it does not uniquely establish that self-report and behavioral risk-taking rely on separate latent representations. The own-choice vectors are extracted from task-specific decision states and may encode board characteristics, decision variables, or numerical response policies rather than general risk propensity.

The limited cross-task transfer (approximately 7%) reinforces this concern. Furthermore, quantity-related directions are potentially part of the intended risk-taking policy itself, since taking more risk is operationalized through choosing larger numbers. Removing these components may therefore eliminate legitimate behavioral mechanisms rather than merely lexical shortcuts.

These issues do not invalidate the intervention results, but they weaken the broader mechanistic interpretation.

Questions for authors
  1. Behavioral validity: Can the authors validate the main steering effects using actually generated decisions rather than conditional answer-token probabilities? In particular, how robust are the BART findings to its low admissible-answer probability mass and alternative behavioral scoring rules?

  2. Representational interpretation: Can the authors distinguish task-specific decision representations from general risk-taking representations, for example through stronger controls for board characteristics or additional cross-task transfer experiments? How can the quantity-related components be separated from legitimate risk-taking policies?

  3. Coherence interpretation: Do anti-aligned compositions produce contradictory absolute self-report and behavioral outcomes, rather than merely opposing changes relative to steering conditions? How do the main anti-coherence rates change when all evaluation cells are included without the self-report endpoint gating?

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2 comments
AuthorsOpenReview ↗

Response to Reviewer r3sE: scoring rules, endpoint gating, own-choice vectors

Thank you for the focused questions. Shared points are answered in the General Response:

  • Generated decisions and BART mass (Q1) in S1–S2
  • Quantity component (Q2) in S3
  • Shared representations and cross-task transfer (Q2) in S6
  • Absolute coherence (Q3) in S4

Here we address the specific unique subpoints the reviewer has raised. We hope this organization is clear and helps avoid duplications.

Alternative behavioral scoring rules (Q1-b)

The family pattern does not depend on the scoring rule. Scoring the same answer-token distribution by its mean number of cards or pumps instead of the threshold gives the same verdict in 93% of the paper's behavioral cells (Spearman ρ = 0.94) and leaves the family pattern unchanged (App. C.5.8). Scoring the decisions the models generate agrees with the answer-token mean as well (r = 0.93 over 48 cells; S1).

Board Characteristic: Own-choice vectors encoding board or decision variables (Q2-b)

Own-choice vectors capture the model's own decision policy; that policy is not tied to the boards it was fit on and carries a weaker risk component beyond the task.

  • Not the boards: recomputed on evaluation rounds absent from the vector's extraction grid, the effect clears the control in 12/12 cells and keeps a median 99% of its size (App. C.5.9).
  • Beyond the task: the vectors also move a binary lottery with no number in the answer (2–4 of 16 cells at the paper's dose, 7–8 at twice it; S3).
  • Rooted in the decision: read over a neutral description of the same boards, they move behavior in only 2 of 16 cells (S5); the direction belongs to making the decision, not to the board text.

None of this reaches risk self-report: with agreement bias removed, own-choice vectors clear BFI in 0 of 16 cells and keep no risk-specific DOSPERT effect (0 of 5; App. C.5.7), which is the dissociation the paper reports.

All cells & no Gating: Reporting rates without self-report endpoint gating (Q3-b)

Without the gate, the conclusion is unchanged: anti-aligned compositions still move the channels apart far more often than aligned ones (Tab. r3sE-A). The gap narrows slightly because the excluded cells (Qwen and OLMo on DOSPERT) have self-report endpoints that do not push toward risk, so their anti-aligned compositions mostly fail to land anti-coherent there. A push-weighted analysis that keeps every cell leaves every per-model rate within 0.03 of its gated value for any weighting constant c ≥ 2 (App. E.1).

Table R3. Rate of anti-coherent administrations under aligned and anti-aligned compositions, with and without the self-report endpoint gate.

AlignedAnti-alignedGap (pp)
With gate (paper)8.5%77.4%68.9
Without gate (all 32 cells)13.0%70.5%57.5
AuthorsOpenReview ↗

Convenience summary: new results from the discussion with other reviewers, relevant to your questions

Thank you again for the focused review. Since our reply, the discussion with other reviewers produced new results that we believe further strengthen our answers to your questions. For your convenience, we summarize here how each point is now addressed (S = sections of the General Response; App. = revised PDF).

Your questionWhat we addedMain resultWhere
Q1. Generated decisions, BART mass, scoring rulesSampled decisions from all four models; BART prompt aligned with CCT's; mean-choice scoringGenerated and answer-token swings agree (r = 0.93, 48 cells); aligned BART prompt raises admissible mass to 96–100% and leaves 48/52 verdicts unchanged; mean scoring gives the same verdict in 93% of cellsS1–S2, App. C.5.8, C.5.10
Q2. Board characteristicsOwn-choice effects recomputed on evaluation rounds outside each vector's extraction gridClears the control in 12/12 cells, keeping a median 99% of its sizeApp. C.5.9
Q2. Cross-task transfer (the ~7%)Absolute transfer to the other risk task and to a new number-free lottery (iKv9 thread, Table R5)The 7% is a ratio against a very large native effect (own-choice: median 44.8 control SDs, vs 6.6 for task instructions). In absolute terms the effects that carry over are comparable: on the other risk task own-choice vectors reach 3.1 (7/16 cells clear) and task instructions 5.0 (9/16); dispositional vectors clear none (0/40)iKv9 thread
Q2. Quantity vs legitimate risk policyBinary lottery with no number to chooseBoth behavior families carry a risk component that generalizes beyond numeric tasks: they move the lottery, where no count is chosen (own-choice 4/16 cells, task instructions 5/16, median 2.1 and 2.2 control SDs), while dispositional vectors do not (0/20, median 0.9)S3, App. C.5.12, iKv9 thread
Representational scopeAbstract revised (in red)Claim scoped to functionally separate directions, not separate latent representationsRevised PDF
Q3. Absolute contradictionsBehavior against the expected-value optimum k*, self-report against the scale midpointWhere composition can shift outcomes in absolute terms, steering creates new absolute contradictions in 20.8% of administrations, and aligned compositions resolve 29.3% of the model's existing ones; the relative effect also survives a band test (49.8% vs 2.3%)S4, App. E.3
Q3. Rates without gatingRates recomputed with the gate removed, over all 32 model × task × instrument × behavior-vector cellsGap remains large: 13.0% aligned vs 70.5% anti-aligned without the gate, against 8.5% vs 77.4% with it (gap 57.5 vs 68.9 pp)Tab. R3, App. E.1

We hope this summary is helpful and gives a clearer picture of how your concerns are addressed. We would be glad to clarify any of these points before the discussion period closes.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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