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Paper summary
The paper examines whether assistants revise their recommendations when a subsequent life event makes an earlier preference inappropriate. It introduces synthetic conversations that distinguish unchanged preferences, explicit revisions, and revisions implied by events. Across nine open-weight models and four API models, the authors find a substantial gap between following explicit updates and inferring implicit ones under the default examination framing. They further examine how this gap varies with context length, deliberation, and conversational framing. Reasoning-trace analysis and Jacobian/R-lens readouts suggest that information supporting an alternative option may be present without determining the final answer. Steering improves implicit updating but can severely impair retention of unchanged preferences.
Critical strengths
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The explicit-versus-implicit comparison provides a useful diagnostic. T0 and T1 test whether models can retain an existing preference and follow an explicitly stated revision, respectively. T2 then tests whether they can infer a revision from an event. The T5 minimal pair helps isolate the effect of including the original preference among the answer options. The gap appears across multiple model families and in both probing and generation settings, making the finding more convincing than a result limited to a single model or response format.
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The framing and steering experiments reveal tradeoffs that would be missed by evaluating implicit-update accuracy alone. Conversational framing improves T2 performance but introduces errors in following explicitly stated preferences. Steering likewise improves T2 while severely degrading T0. These results show why improving performance in one condition does not necessarily yield a better preference-following system overall.
Critical weaknesses
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The human validation does not fully resolve this concern. Table 17 reports 75% agreement with the answer key on 20 T2 items evaluated by one annotator. The reported 100% ceiling is based on the 15-item subset for which that annotator endorsed the premise; the stricter subset contains only 10 items. These results support the existence of clear model failures on some examples, but leave the validity of the benchmark’s labels more broadly uncertain. Independent validation, with results reported separately for push and pull events, would strengthen the central claim.
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The steering results also appear consistent with suppressing the original preference, given the collapse in T0 accuracy. They therefore provide limited evidence that the intervention selectively restores a correctly computed update. Finally, the abstract and Section 7 discuss activation patching, but I could not locate its experimental setup or quantitative results in the manuscript. This makes that part of the causal argument difficult to assess.
Questions for authors
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How much of the behavioral gap remains on push-only items with independently validated premises? Please report these results separately from those for pull items. Does the human–model gap remain large when evaluation is based on agreement among independent annotators, rather than a subset selected using a single annotator’s premise judgments?
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Can the event-token readout distinguish between events within the same attribute that support different recommendations, or between events that make an option inappropriate and those that merely mention it? Appendices C/I identify this missing control. Such comparisons would help establish whether the readout captures an updated preference rather than an association with an option.
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(2/4) Q1 and W1. The behavioural gap on push items with independently validated premises
The main result remains. Two more independent annotators have completed the same 60 items, so we can now assess the premises using agreement between three readers rather than one reader's judgment.
The annotators agree on the answer for 91.7% of all 60 items (Cohen's κ=0.91) and 85.0% of the 20 T2 items (κ=0.84). They agree on the premise check for 96.7% of items (κ=0.93). For the clearly-better check, raw agreement is 86.7%, while κ is 0.44. This lower κ reflects the high base rate of "yes" responses. All five answer disagreements occur in T2 and T4, where the premise is contestable.
The table below reports results by event type for the new annotators. Each gate requires agreement between both annotators.
| Gate | Force | n | Annotator A | Annotator B | Models |
|---|---|---|---|---|---|
| Both accept premise | Pull | 7 | 100.0% | 85.7% | 1.0% over 104 |
| Both accept premise | Push | 8 | 100.0% | 87.5% | 14.3% over 98 |
| Both gates | Pull | 4 | 100.0% | 100.0% | 1.5% over 66 |
| Both gates | Push | 6 | 100.0% | 100.0% | 2.9% over 70 |
On the subset where both annotators accept the premise and agree that the alternative is clearly better, both answer every item correctly for both event types. Models reach only 1.5% on pull and 2.9% on push. Pooled across event types, both annotators score 100% on these 10 items, compared with 2.2% for the models. Models are evaluated on exactly the same items that pass each gate.
Every human error by either annotator selects the original stated option, despite that annotator having marked the premise as disputed. These are disagreements with the answer key, not failures to infer the implied preference.
Results across the full item set
The following table reports the T2 results from our main table, split by event type using the same hand annotation, items, and parser. The pooled column reproduces the main table. Chance is 50%.
| Model | Readout | Pull | Push | Pooled | p |
|---|---|---|---|---|---|
| Qwen3.5-0.8B | Probe | 2.9 (n=276) | 3.2 (n=186) | 3.0 | 1.000 |
| Qwen3.5-2B | Probe | 3.3 (n=276) | 2.7 (n=186) | 3.0 | 0.789 |
| Qwen3.5-4B | Probe | 0.7 (n=276) | 4.3 (n=186) | 2.2 | 0.017 |
| Qwen3.5-9B | Probe | 2.5 (n=276) | 9.7 (n=186) | 5.4 | 0.001 |
| Qwen2.5-7B | Probe | 10.1 (n=276) | 13.4 (n=186) | 11.5 | 0.299 |
| Qwen3.5-2B | Gen. | 2.7 (n=74) | 2.4 (n=42) | 2.6 | 1.000 |
| Qwen3.5-4B | Gen. | 0.0 (n=76) | 6.8 (n=44) | 2.5 | 0.047 |
| Qwen3.5-9B | Gen. | 1.8 (n=166) | 8.1 (n=74) | 3.8 | 0.027 |
| Qwen2.5-7B | Gen. | 12.7 (n=166) | 14.9 (n=74) | 13.3 | 0.683 |
| Gemma-3-1b | Gen. | 14.5 (n=76) | 0.0 (n=44) | 9.2 | 0.007 |
| Gemma-3-4b | Gen. | 2.6 (n=76) | 4.7 (n=43) | 3.4 | 0.619 |
| Gemma-3-12b | Gen. | 5.3 (n=76) | 15.9 (n=44) | 9.2 | 0.096 |
| Gemma-3-27b | Gen. | 2.6 (n=76) | 13.6 (n=44) | 6.7 | 0.050 |
| gpt-5.4-nano | Gen. | 0.0 (n=276) | 0.0 (n=186) | 0.0 | 1.000 |
| gpt-5.4-mini | Gen. | 2.5 (n=276) | 5.4 (n=186) | 3.7 | 0.133 |
| gpt-5.4 | Gen. | 12.3 (n=276) | 15.1 (n=186) | 13.4 | 0.407 |
| gpt-5.6-sol | Gen. | 14.5 (n=276) | 33.3 (n=186) | 22.1 | <1e-5 |
The gap is at least as large on push as on pull for every model except Gemma-3-1b, the weakest model in the study. The highest push result is 33.3% for gpt-5.6-sol, still below chance. Eleven of the seventeen rows are below 10%.
This distinction matters for interpreting the mechanism results. Our event-token measurement cannot resolve push events, but the behavioural evaluation does not share that limitation. In fact, models perform slightly better on push than pull behaviourally. The event type our mechanism analysis cannot resolve is therefore not the one driving the behavioural result.
(3/4) W2b. Activation patching is discussed, but its results are missing from the manuscript
The reviewer is right, and we apologise. We removed the section reporting the patching setup and results to meet the page limit but left the related claims in the abstract and Section 7. We provide the setup and results here.
Setup. We patch the inference-specific component rather than the full activation:
δᵢ = h_ev(i) − h_ev(i with a mismatched event)
This is the same per-item quantity validated by our event-token control. It is not deployable by construction because computing δᵢ requires the item's own twin. The experiment is therefore a mechanism test comparing three intervention arms, each applied at the answer token:
- The item's own
δᵢ. - A different item's
δ, matched in norm. - A Gaussian vector, also matched in norm.
We test three layers per model, with α up to 2 and 30 items per condition.
Results. Both model families show a null result. On Gemma-3-12b, the item's own δ moves T2 accuracy from 10.0% to at most 20.0%. A different item's δ reaches 20.0%, while a norm-matched Gaussian reaches 21.7%. On Qwen3.5-9B, all three arms move accuracy from 3.3% to 5.0%, with mean margins differing by no more than 0.2.
The effect therefore does not depend on the item's own inference. These results do not establish the causal transport claim, and we will remove that claim.
Positive control. We also test whether the intervention setup can produce a measurable effect. Since
lensₗ(h) = unembed(Jₗh)
the steepest-ascent direction for our margin at layer l is
vₗ = Jₗᵀ(U_c − U_d)
Applied at the answer token, this direction produces a strong effect in both model families.
On Gemma-3-12b at layer 36, T2 accuracy rises from 10.0% to 100% at α = 0.10, while the margin increases from −6.26 to +12.41. At layer 21, the same intervention reaches only 56.7%, showing that the effect varies with depth.
On Qwen3.5-9B at layer 24, accuracy rises from 3.3% to 55.0%, and the margin increases from −4.15 to +0.27. Random directions leave Qwen at 3.3% throughout.
This positive control shows that the setup can detect an effect at these sample sizes. The patching null is therefore specific to the tested vector, rather than a general limitation of the method. However, this direction is not a proposed repair as it uses the unembedding row for the correct answer and cannot be computed without knowing that answer.
(1/4) Q2. Can the event-token readout distinguish same-attribute events that support different recommendations?
We thank the reviewer. Both questions identified missing controls, and we ran both experiments. Two new independent annotators have also completed the validation set, addressing the first weakness. The remaining weakness was a production error on our side: activation-patching results were omitted from the manuscript even though the abstract and Section 7 still refer to them. We provide the missing results below.
Our submitted control paired each T2 item with a twin whose event came from a different attribute. As the reviewer notes, this could not distinguish whether the readout tracks an updated preference or simply an association with a topic.
We reran the control using donor events from the same attribute, but implying a different one of the three preference states. Both prompts therefore concern transit or exercise and differ only in which option the event supports. The conversation, turn-1 statement, option pair, and seed remain fixed.
The effect becomes stronger, not weaker.
These values are paired differences in the event-token margin against each item's twin, using the same layer band and readout as the main mechanism table. The reported p-values use a two-sided Wilcoxon signed-rank test; the final column uses a Mann-Whitney test between subgroups.
Across all 120 items, the paired difference increases from +5.53 to +8.61 on Gemma-3-12b (p=7e-7, 88/120 items positive) and from +0.81 to +1.31 on Qwen3.5-9B (p=9e-7, 83/120 items positive). The ballot effect at the answer token remains unchanged at +20.09, confirming that the rest of the pipeline is unchanged.
Matching the attribute strengthens the contrast. This supports the interpretation that the event-token readout tracks which option the event points to, rather than simply the topic.
This result also requires us to revise our explanation of the push null. We had attributed it to the donor event being topically unrelated to either option. Since matching the attribute does not resolve the push null, that explanation is no longer supported.
The remaining possibility is that the readout tracks the specific option, which the donor event does not mention. A cleaner test would pair each eliminating event with a same-topic event that does not eliminate the option, such as "I finally got the bike serviced" versus "I fractured my wrist". This would isolate elimination while holding the topic fixed. We have not built these stimuli, so we cannot yet establish this explanation. We will state this limitation explicitly rather than retain the weaker explanation.