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Paper summary
This paper addresses the task understanding bias in LLM intelligent agent communication and proposes Proactive Understanding Risk (PIR) to guide message rewriting and information querying. This method evaluates both understanding and execution results, utilizes offline supervised learning for risks, and combines historical interactions to infer the type of the recipient. Experiments on six knowledge base question-answering datasets and five recipients show that this method can improve risk calibration and reduce understanding failures; theoretical analysis discusses when the recipient's information is helpful for communication decisions. However, the rewriting benefits mainly come from universal fixes applicable to all recipients, while the benefits of active querying are small and do not lead to a stable increase in task success rate.
Critical strengths
- The paper clearly distinguishes between "understanding the wrong task" and "understanding the correct task but failing to execute it", and places risk prediction before message transmission. This perspective is more detailed than simply judging the communication quality based on the final answer, and also provides a reasonable conceptual basis for different intervention methods such as message rewriting and capability enhancement.
- The author systematically studied the differences among recipients through the same message, multiple frozen recipients, randomization of probe wording, and option sequence. The probe and execution were independently called, avoiding direct indication of the execution branch by the candidate task. The data were divided by question groups, and the calibration and main evaluation retained the natural error rate, reducing the evaluation bias caused by the enrichment of rare failure samples.
- The method retains the uncertainty of the receiver's identity and selects the message based on the posterior expected loss, rather than prematurely adopting a single identity guess. VoII further distinguishes between "information that is helpful for identifying the receiver" and "information that can improve message selection". The fixed candidate set before and after the query also enables the separation of information value from the benefits of random candidate generation.
Critical weaknesses
- The paper measures whether the recipients have understood the original message through task recognition probes. However, when recognizing after seeing the candidate tasks, the understanding formed is not exactly the same as that when directly executing the original message. Independent probes and execution calls avoid direct hints from being leaked, but they cannot confirm that the two correspond to the same potential understanding state. The authors have analyzed the deviation of option positions and proved that after controlling this factor, the heterogeneity of recipients still exists; however, this does not yet fully establish the correspondence between probe labels and the task understanding in actual execution.
- The author points out that each receiver calibration can restore most of the predicted benefits, and reports that the complete model still has a small but significant additional sorting improvement. However, whether the incremental improvement in the prediction indicators is sufficient to improve message selection and queries remains to be directly verified. In Experiment 4, the results of uniform receiver beliefs, posterior inference, and true identities are almost the same; the author explains this as the candidate message preferences being basically consistent, but it also means that this experiment mainly verified the general repair, and the incremental value of receiver-specific modeling in downstream decisions is still unclear.
- The author's mechanism analysis indicates that the main rewriting benefits come from clearly stating the expected output, and this fix is helpful for all recipients. The existing general clarification rewriting baseline does not specifically implement this operation, so the complete method is superior to it. It is still not possible to distinguish whether the benefits come from the learned risk guidance or from a directly applicable output description rule.
- VoII achieved a statistically significant but relatively small absolute improvement in the understanding metrics on the main queue; the authors also explicitly reported that the improvement range of the replicated queue included zero, and the task success rate did not show a stable increase; in some settings, it even decreased. Therefore, the current evidence supports that VoII has a certain effect on the optimized understanding metrics, but it has not yet established a reliable benefit for the overall task.
- The experiment mainly utilized fixed template knowledge base questions, two types of task comparisons, five known recipients, and a maximum of one fixed database query. Such controls were conducive to isolating recipient differences, but were insufficient to test the risks of intermediate result handover, multiple constraints, tool parameters, and multi-round interactions, nor did they test unknown recipients or configuration changes.
Questions for authors
My concerns are shown in the weaknesses.
6 comments
From receiver-specific prediction to message decisions
Thank you for asking how prediction gains affect message choice. Your question helped us test the next decision directly.
W2: From prediction gains to decision value.
The revised Experiment 2 text now points to Experiments 4 and 5 for the message and query tests. We give risk calibration, candidate generation, message selection, and query value their own evidence.
W2: Risk calibration. Receiver information mainly corrects the risk level of each receiver. The receiver-calibrated version of the receiver-agnostic model recovers most of these gains.
| Gain recovered by recalibration | Share (%) |
|---|---|
| ECE reduction | 93 |
| Across-receiver AUROC gain | 96 |
Appendix I.2 reports this result and richer calibration controls. Much of the across-receiver difference reflects receiver levels, including Nemotron's option-position effect.
The full model adds a small ranking gain within receivers relative to receiver recalibration.
| Prediction metric | Gain |
|---|---|
| AUROC | +0.004 |
| AUPRC | +0.007 |
These intervals support a prediction difference on the probe endpoint. The message and query experiments measure the next two decisions directly.
The sender computes expected loss by averaging candidate risks over the receiver belief. This makes receiver risk levels relevant to its calculation. Useful action changes also require differences between candidate messages. We have removed the main-text wording that equated pooled prediction ranking with the sender's decision. The new wording points to the separate message and query experiments.
W2: Message generation and selection. The original Experiment 4 gives:
| Condition | Probe error (%) |
|---|---|
| Guidance alone | 2.29 |
| Full method | 2.31 |
| True identity | 2.30 |
The decision checks are:
| Panel / comparison | Result |
|---|---|
| Original E4: uniform vs inferred belief | 2 of 7,895 decisions changed |
| Added paired panel: full vs first valid guided | 94.26% identical messages |
These results point to shared repair as the main source of the gain.
The candidate analysis identifies a shared repair. An unstated output is the top learned risk feature for every receiver. Among changed messages sent by the full method, 97% keep the question and add an output line. Most generic rewrites leave the output unstated. Thus the main observed rewriting gain comes from improving the candidates in a way that helps all receivers.
W2: Direct checks of decision value.
We have added two direct checks. Appendix I.4.1 compares full selection with a fixed output rule that has no learned risk model. Appendix I.5.1 tests querying on a fixed guided pool. Differences are in percentage points, each comparison uses its own paired panel.
| Setting / contrast | Endpoint | Difference |
|---|---|---|
| Fixed-output test: full minus fixed | Probe error (primary) | -0.132 |
| Guided pool: query minus no query | Probe error | -0.001056 |
| Guided pool: query minus no query | Net utility | -0.003808 |
The fixed rule itself improves over the original.
W2: What the theory and evidence support.
The theory in Section 4 provides a useful way to read these findings. Different receiver error rates do not ensure that receivers prefer different messages. With exact losses, a shared best message can leave no decision value for extra receiver information. Positive value requires information that improves the message choice. The theorem uses exact losses. Our direct tests assess the fitted controller with measured outcomes.
This distinction strengthens the practical use of the framework. It lets a reader ask three separate questions: Is the risk estimate well calibrated? Does receiver information improve the message choice? Does paying for another query improve that choice enough to cover its cost? Our results give strong evidence for receiver-dependent calibration and a useful shared repair.
A direct baseline for the shared output repair
Thank you for highlighting the need to test the shared output repair with a simple rule. This helped us add a direct comparison with the full method.
W3: A direct test of the fixed output rule.
We have added the fixed explicit-output baseline in Appendix I.4.1 and reported its main paired result in the Experiment 4 text. This directly tests your concern: can the shared repair be obtained by a simple output rule with the same intent information and checks, without learned risk guidance? The fixed rule recovers most of the measured rewrite gain.
The rule keeps the original question word for word and adds one sentence stating the required output. The writer receives the same sender intent. It generates four candidates and uses the same semantic-verifier prompt and original validity checks. It sees no receiver identity, posterior, learned risk score, or gold answer. We send the first valid candidate. If all candidates fail the checks, we send the original. There is no risk-based ranking and no new generation after semantic rejection.
The comparison uses 1,579 questions, 1,578 frozen question groups, and five receivers. Four conditions were measured together: original, fixed output, guided first valid, and full selection. Each distinct message-receiver pair has 36 probes, covering six wordings and all six option orders, plus one separate answer call. Equal messages share their measurement. The frozen primary rule counts None and unparsed replies as errors.
W3: Paired results.
The added panel gives:
| Condition | Probe error (%) |
|---|---|
| Original | 4.144 |
| Fixed output | 2.432 |
| First valid guided candidate | 2.274 |
| Full selection | 2.300 |
Paired differences are in percentage points
| Contrast / endpoint | Difference |
|---|---|
| Full minus fixed / probe error (primary) | -0.132 |
| Fixed minus original / probe error | -1.711 |
| Full minus fixed / answer failure (secondary) | -0.659 |
Both intervals for the primary probe comparison include zero. The fixed rule itself lowers probe error from the original. This is direct evidence for the value of keeping the question and stating the output. It also explains why a generic clarity rewrite is too weak a baseline for this specific mechanism. The new baseline makes that comparison explicit.
The answer-failure comparison is a secondary, pointwise result without correction for multiple tests. We include it alongside the main result and keep its status clear.
W3: Analysis and writer source.
The table reports both uncertainty analyses. The original analysis uses 10,000 paired question-ID resamples and keeps all receiver pairs within each question. The added sensitivity check resamples whole frozen question groups. It retains equal question weights, so the point estimate is unchanged. Because dataset sizes differ, this is a question-weighted result across the six datasets, not an equal-dataset average.
We also give the candidate source details beside the table. The fixed and guided pools used the same hosted writer name and generation settings. The guided pool was generated on September 24 and the fixed pool on November 7, through different providers. Most records have no model fingerprint. The comparison uses these stored pools and fresh paired receiver measurements collected together for all four conditions.
This is an added panel, so its rates differ slightly from the archived Experiment 4 table. We keep both panels labelled and make paired comparisons within each one. The new panel also gives:
| Message comparison | Identical decisions | Share (%) |
|---|---|---|
| Full vs first valid guided | 7,442 / 7,895 | 94.26 |
This count concerns the selector's effect after guided generation; it is separate from full-versus-fixed message agreement.
The revised claim is useful and specific. A shared explicit-output repair explains much of the measured rewriting gain. The learned feature analysis helped identify that repair, and the direct baseline shows how much a simple rule can recover. The full-versus-fixed comparison measures the next step after shared repair. This lets readers use the practical repair while judging the added model components on direct evidence.
Task identification and interpretation during execution
Thank you for pointing out the gap between probe choices and interpretation during execution. This helped us add behaviour checks and state the measurement conditions.
W1: Probe validity and separate calls.
We agree that showing task options can affect how a receiver reads a message. Separate calls avoid leaking those options into execution, but they do not reveal the internal task state of that execution. We have revised Sections 2 and 3 and added the direct behaviour checks in Appendix D.4.
Section 2 now defines the measured endpoint. The probe asks the receiver to choose the intended task, one contrast task, or "None of these/unclear". None records rejection or uncertainty and is stored separately from contrast choices. Both count as errors. Repeated choices form a soft target under the stated options, wordings, and parsing rules. This is a task-identification risk that can be predicted before sending.
W1: Behaviour checks and option position.
We checked its link to actual outputs. A blinded Qwen judge labelled archived QA replies by the task they appeared to attempt, separately from factual correctness. The main audit covers 6,629 questions and five receivers, or 33,145 pairs; 31,966 could be assigned to the intended or contrast task. The table gives contrast-task behaviour differences between pairs with any probe error and pairs with none, in percentage points.
Excluding Qwen uses the same judge on the other receivers. Coverage is the share assigned a task label, not the judge's accuracy. The separate 900-question check has an interval that includes zero. Balancing option positions makes their weights equal; it does not remove the effect of offering choices.
We also report a controlled action holdout. A fixed interpreter records operations and arguments, which helps separate the attempted task from factual answer correctness. It has 48 components and 480 execution units; 449 could be assigned to one of the two task operations. Appendix D.4 now defines the task pairs, Brier calculation, and component bootstrap. The other 31 units use operations outside the pair and stay in the coverage count. The probe prediction is the number of contrast-task choices divided by six. None choices stay in the total of six. The execution label is 1 for the contrast task and 0 for the intended task. The Brier difference is averaged over four task cells fixed before testing.
Lower Brier is better, so this favours the simple baseline. The revised appendix reports both the QA association and this calibration gap.
Appendix D.3 also retains the position result.
That supports receiver differences within the measured protocol. It does not by itself validate the probe as a measure of interpretation during execution.
W1: Assumptions and the interpretation of the results.
The bridge to latent PIR needs valid task descriptions, controlled measurement error, and comparable task interpretations across probe and execution calls. It also needs suitable handling of rejection and unparsed replies. The offered task choices may change the interpretation they are meant to measure. A visible wrong operation may also result from an execution error. The added checks give evidence about these links, while leaving the full latent state unobserved.
Eq. (4) conditions action failure on correct interpretation in the same execution. Section 3 now states the required measurement model. It must link separate probe choices to interpretation and action in that execution. The execution head learns answer errors under probe-correct weights. Using this head to estimate Eq. (4) requires that joint link.
We have also changed the Experiment 1 text, figure labels and captions, and table headings. The reported 32% now refers to soft probe-error weight paired with success in an independent answer call. The text and figures now use this cross-call meaning throughout. These revisions keep the main idea precise. Task identification and final-answer checks provide different observable information. The paper now tests their relation directly and states the conditions needed to interpret a probe score as latent misunderstanding risk.