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Paper summary
The paper compares models' predictions of a human reader's affect with their own prompted numerical affective reports. It studies four small model families using probing, representational alignment, and activation interventions. Reader and Self outputs are strongly correlated, and affect-related information is decodable in both tasks. However, the tested interventions do not establish reliable cross-task transfer or robust control of self-report. The state-induction gate fails for both valence and arousal, and the later layer/token-position analyses are presented as exploratory.
Critical strengths
- The distinction between output similarity, decodability, and causal use is worth studying. The experiments use matched stimuli with separate prompts, held-out probes, random-donor controls, and discovery/confirmation splits. These controls are useful because a correlation between Reader and Self outputs would otherwise be easy to overinterpret.
- The authors are open about unsuccessful interventions and variation across models. They report the failed gate, label subsequent analyses as exploratory, and do not equate numerical self-reports with subjective experience. The matched-plain Base/Instruct comparison also addresses an obvious prompt-format confound.
Critical weaknesses
- I am concerned that the output scoring could make intervention effects look artificially small. Appendix C.8.1 averages token log-probabilities and then applies softmax over JSON candidates. This is not the usual probability distribution conditioned on that candidate set. With equal candidate length m, it is equivalent to using temperature m on the summed sequence scores, which flattens the distribution. V1 effects are often around 10^-3 on a 1–9 scale (Tables 21–22), while the separate V3 analysis uses fixed .1 and .05 thresholds for sufficiency and specificity. These stages have different candidate spaces, so the numbers should not be directly equated; the concern is that the same scoring transformation is used throughout. Results under alternative scoring and calibration against natural stimulus effects are needed before interpreting failed thresholds as weak causal control.
- The negative results leave several mechanistic explanations open. Raw cross-task patching can fail because of coordinate differences, task offsets, or off-manifold interventions. Table 19 itself shows very poor direct cross-decoding and improvement after alignment. A failed intervention therefore establishes a limit of that intervention, not necessarily an intermediate mechanism between fully shared and fully independent processing. The discussion sometimes makes this stronger inference despite acknowledging the alternatives elsewhere. The generation-stage result is also measured along a fixed, teacher-forced neutral JSON response. It does not yet establish a mechanism that can support selective control in natural dialogue.
Questions for authors
- Do the main behavioral and intervention conclusions persist using summed sequence log-likelihoods, several softmax temperatures, and natural/free-generation readouts? Please report effect sizes relative to the clean Clinical–Neutral shifts as well as absolute thresholds.
- Can you show calibration with a positive-control intervention that reliably changes the measured affect score, and report all gate estimates and confidence intervals? The present Appendix Q contains no results table, making the gate and replication claims difficult to audit.
- Does cross-task causal transfer improve after training-only alignment or task-offset correction? Such results would help distinguish a coordinate mismatch from a lack of shared causal information.
- Please reconcile the direction of the H1 replication criterion: Appendix P.49 prints confidence bounds greater than zero for causal-minus-decoding depth, while the main text describes replication of Qwen's negative depth difference. Which signed statistic was actually tested?
6 comments
W2. Alternative explanations for negative results and teacher forcing
We agree with the reviewer. A failed intervention primarily indicates the limits of that intervention and measurement procedure, and does not directly prove the absence of a shared mechanism.
Because E4 injects Clinical–Neutral differences, mean offsets between tasks cancel by construction. The cosine similarity between the Reader-derived injection vectors and Self's own differences was 0.571–0.957 for matched stimuli and 0.069–0.143 for random stimuli.
On the other hand, the possibility of off-manifold interventions remains. In a simple diagnostic using Mahalanobis distance, the proportion of intervened states exceeding the 95th percentile of real Self states was 34% for Qwen Base and 67% for Gemma Instruct. For the random control, it was even higher at 69–92%, which introduces the additional limitation that the degree of off-manifold deviation differs between the conditions being compared. This diagnostic also depends on shrinkage estimation of the covariance.
More importantly, even the within-task Self→Self positive control produced effects only on the order of . This suggests that the E4 measurement procedure may have lacked the sensitivity to detect causal transfer at the tested intervention site.
Accordingly, we withdraw the interpretation that the results "support an intermediate mechanism between fully shared and fully independent processing." What we can currently show is only that the predictions of a simple shared model were not supported under the tested intervention conditions.
We also withdraw the statement, based solely on the V2 alignment results, that the differences "cannot be explained by linear coordinate mismatch."
Regarding teacher forcing, our generation-stage analyses were performed on a fixed neutral JSON sequence. Up to pre_V for Valence, the prefix is shared across all candidates, but Arousal and later generation stages depend on the preceding tokens.
In the revised version, we will position these results as exploratory findings conditional on the specific response format and generation positions, and will not claim to have demonstrated selective causal control in natural dialogue.
Q1. Do the main conclusions persist under alternative scoring?
At present, we cannot claim that all conclusions persist under every scoring method.
For behavioral coupling, we re-analyzed 4 of the 8 models with alternative scoring. Under summed sequence log-likelihood scoring, positive Reader–Self change correlations were observed for each of Valence, Arousal, and Dominance.
However, partial correlations after controlling for Writer shrank to 0.09–0.47, and in some conditions the confidence intervals included zero. In addition, the mode is discrete and carries little information, and in some conditions the correlation could not be computed.
For Qwen Base, the magnitude of the correlation coefficients differed substantially between the original scoring and the mode. Invariance of effect sizes across scoring methods has therefore not been demonstrated.
For the V3 Gate, all 12 alternative scores evaluated on Qwen2.5-1.5B-Instruct yielded NO_GO. However, the direction vectors were fixed to those estimated under the original scoring.
Effects relative to the natural stimulus changes were 0.039–0.329 for V1 and 1.8% (Valence) and 0.2% (Arousal) for V3 Gate Sufficiency. These are results under the original scoring; relative intervention effects under alternative scoring have not been verified.
Measurement under free generation, formal scoring comparisons for the remaining 4 models, and re-estimation of direction vectors based on alternative scores have also not been completed.
In the revised version, we will distinguish verified results from unverified scope, retain the main-analysis decisions based on absolute thresholds, and add the post-hoc sensitivity analyses.
Q2. Positive control and Gate estimates/confidence intervals
As the reviewer points out, Appendix Q in the submitted version was missing the necessary quantitative results. In the revised version, we will restore all estimates, 95% confidence intervals, thresholds, and decisions.
Results for Qwen2.5-1.5B-Instruct, L14, prompt_end, and 58 test stimuli are as follows:
| Metric | Valence (95% CI) | Arousal (95% CI) |
|---|---|---|
| Sufficiency | 0.00129 [0.00043, 0.00212] | 0.00017 [−0.00005, 0.00039] |
| Specificity | −0.00147 [−0.00248, −0.00044] | −0.00011 [−0.00042, 0.00022] |
| Endogenous AR | −0.0075 [−0.0366, 0.0216] | 0.0082 [0.0013, 0.0162] |
| Topic TVD | 0.0036 [0.0031, 0.0043] | 0.0039 [0.0033, 0.0045] |
The prespecified decision criteria were: the lower bound of the 95% CI for Sufficiency > 0.1, Specificity > 0.05, Endogenous AR > 0.05, and the upper bound of the 95% CI for Topic TVD < 0.15.
Under these criteria, both Valence and Arousal were NO_GO. In particular, the lower bound of the confidence interval for Specificity was negative on both axes, so the decision would not change even if the threshold were lowered to 0.
On the other hand, the submitted version did not include a sufficient positive control to verify measurement sensitivity. Calibration via full replacement with Clinical activations or stronger interventions has not been performed.
Therefore, the current NO_GO means that the criteria were not met at the specified site, intervention method, and scoring procedure. It does not guarantee that the measurement procedure can detect every valid causal intervention.
In the revised version, we will restore Appendix Q and state this limitation explicitly.
Q3. Does cross-task causal transfer improve with alignment or offset correction?
At present, we have not demonstrated that alignment or offset correction improves cross-task causal transfer.
Because E4 injects difference vectors, mean offsets between tasks cancel. In addition, vector directions after Procrustes alignment computed from the existing representations did not differ substantially from those before alignment.
However, these results do not test causal transfer after alignment itself.
As the reviewer suggests, an experiment that learns the alignment on the Discovery data, performs absolute-state replacement including offset correction, and evaluates within-task replacement as a positive control has not been conducted.
Therefore, we cannot currently conclude to what extent coordinate-system mismatch contributed to the failure of causal transfer. In the revised version, we will revise the text so as not to draw strong mechanistic conclusions from the failure of direct transfer.
Q4. Sign of the H1 replication criterion
We thank the reviewer for pointing out this important inconsistency.
In the actual analysis, we defined the difference between the causal peak depth and the decoding peak depth as , multiplied it by a sign chosen to match the direction observed in Qwen, and used as the criterion that the lower bound of the 95% confidence interval of exceeds zero.
For Valence, for both peak and COM; for Arousal, for peak and for COM.
However, Appendix P.49 retained the criterion before sign alignment. This is a descriptive inconsistency.
More importantly, the sign-aligned criterion was introduced after the replication results for the other model families had been computed, and was not fixed in advance.
The actual results are as follows:
- Under the sign-aligned criterion, Llama and OLMo passed for Valence, while Gemma failed. For Arousal, all three families failed.
- Applying the criterion as written in Appendix P.49, all three families failed.
- The Valence passes for Llama and OLMo arise from causal peaks located at layer 0, which is qualitatively different from the peak at relative depths of approximately 0.74–0.78 observed in Qwen.
Therefore, we do not claim that the depth dissociation observed in Qwen was replicated in the other model families.
In the revised version, we will correct the test statistic and the treatment of the sign to match the implementation, and report results under both criteria. We will also state when the criterion was introduced, and revise the statements about replication to partial, exploratory findings.
We thank the reviewer for the careful review and important comments. In particular, we re-examined the effect of the scoring procedure on estimated intervention effects, alternative explanations for the negative results, the lack of a positive control, and the replication criterion for H1. Below, we present the additional analyses and planned revisions.
W1. Shrinkage of effects due to scoring and fixed thresholds
The reviewer's point is mathematically correct.
Within each model and candidate space, all candidates have equal token length, and the softmax over mean log-likelihoods is equivalent to applying temperature T=m to summed sequence log-likelihoods. The candidate length m is 10, 12, 15, or 17 depending on the model family and candidate space, so there is the additional issue that the effective temperature differs across model families.
For Qwen Base with the 729-candidate space, the mean entropy of the distribution obtained from mean log-likelihoods was 6.590 nats, very close to the 6.592 nats of the uniform distribution. The original scoring therefore substantially flattens the candidate distribution.
In additional sensitivity analyses, the Reader–Self change correlations for Qwen Base (Valence/Arousal) were 0.809/0.866 in the main analysis, 0.880/0.911 under summed sequence log-likelihood scoring, and 0.441/0.442 under mode-based scoring. The sign of the correlations was preserved and none of the 95% confidence intervals included zero, but the effect sizes depended on the scoring method.
In addition, partial correlations controlling for Writer changes were substantially lower, so these results cannot demonstrate sharing of task-specific affective processing.
Intervention effects should likewise not be interpreted on the absolute scale alone. The median ratio of V1 intervention effects to the natural Clinical–Neutral changes was 0.039–0.329. In contrast, the point estimate of Sufficiency for the V3 Gate was 1.8% (Valence) and 0.2% (Arousal) of the natural displacement. However, because V1 uses a 729-candidate space and V3 an 81-candidate space, their absolute values cannot be compared directly.
Furthermore, the V3 Sufficiency threshold of 0.1 was larger than the natural displacement of the target model, 0.072 (Valence) and 0.085 (Arousal), and was thus not properly calibrated.
To examine this issue, we evaluated 96 threshold settings under the original scoring, and no setting yielded GO. We also re-evaluated the Gate for Qwen2.5-1.5B-Instruct using 12 alternative scoring methods, and all were NO_GO for both Valence and Arousal.
However, in the alternative-scoring analyses, the intervention directions were fixed to those estimated under the original scoring; re-estimating the direction for each score has not been tested. In addition, all of these are post-hoc sensitivity analyses and do not replace the confirmatory results of the main analysis.
In the revised version, we will clearly describe the flattening caused by the scoring procedure, the effective temperature, comparisons against natural displacement, and the distinction between threshold sensitivity and scoring sensitivity. We retain the Gate's NO_GO as a decision under the specified measurement and intervention conditions, but do not interpret it as implying that causal control is impossible in general.