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Under review as a conference paper at ICLR 2027

Prospective Interpretation Risk: Predicting and Preventing Miscommunication Between LLM Agents

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Abstract

Large language model (LLM) based agentic systems increasingly rely on models communicating with one another, yet existing uncertainty and multi-agent methods rarely estimate how a particular receiver will interpret a message before it is sent. This matters in heterogeneous systems, where capable receivers can reconstruct different tasks from the same message. We model this as a sender–receiver problem with a latent receiver type and define prospective interpretation risk (PIR): the probability that a receiver reconstructs a task other than intended. Rather than model an LLM's full input–output behaviour, we use black-box probes relating messages, intended tasks, and receiver-specific reconstructions, yielding scalable supervision while separating interpretation from downstream capability failure. Offline, heterogeneous frozen receivers provide supervision for receiver-conditioned risk and the effects of predefined mutable message features. At deployment, history induces a posterior over receiver types, guiding message revision and selection. We further introduce value of interpretation information (VoII), querying for receiver information only when its expected communication benefit exceeds its cost. Our theory characterises when receiver information has decision value and bounds such queries. Empirically, interpretation-failure rates vary by 4–13 across receivers. Receiver information reduces PIR calibration error by 68% relative to a receiver-agnostic predictor, largely by correcting receiver-specific risk levels. PIR-guided revision reduces interpretation failure by 44% relative to the original message and 40% relative to a generic rewrite, mostly through a repair that helps every receiver. VoII outperforms information-gain and random querying at matched cost on the interpretation objective it optimises, lowering interpretation failure from 3.84% to 3.79% while querying 18.2% of episodes.

Primary area:
foundation or frontier models, including LLMs
Keywords:
uncertainty estimation, bayesian modelling, LLMs

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_9ScsOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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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
  1. 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.
  2. 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.
  3. 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
  1. 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.
  2. 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.
  3. 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.
  4. 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.
  5. 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
AuthorsOpenReview ↗

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.

QA checkDifference (points)
Main audit1.621
Excluding Qwen receiver1.414
Separate position-balanced check, 900 questions0.643

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.

Action checkBrier difference
Probe minus always-intended+0.012743

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.

Position resultValue
Nemotron error, intended option lastAbout 24.5%
Nemotron error, intended option first or second3.8%
Highest/lowest receiver error, first or second3.8 times

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.

AuthorsOpenReview ↗

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 recalibrationShare (%)
ECE reduction93
Across-receiver AUROC gain96

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 metricGain
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:

ConditionProbe error (%)
Guidance alone2.29
Full method2.31
True identity2.30

The decision checks are:

Panel / comparisonResult
Original E4: uniform vs inferred belief2 of 7,895 decisions changed
Added paired panel: full vs first valid guided94.26% 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 / contrastEndpointDifference
Fixed-output test: full minus fixedProbe error (primary)-0.132
Guided pool: query minus no queryProbe error-0.001056
Guided pool: query minus no queryNet 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.

AuthorsOpenReview ↗

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:

ConditionProbe error (%)
Original4.144
Fixed output2.432
First valid guided candidate2.274
Full selection2.300

Paired differences are in percentage points

Contrast / endpointDifference
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 comparisonIdentical decisionsShare (%)
Full vs first valid guided7,442 / 7,89594.26

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.

Reviewer_5dn1OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper addresses the important problem of effectively conveying information between LLMs, particularly when a task is handed off from one to another. In particular, it introduces prospective interpretation risk (PIR) for LLMs, the probability that a receiver reconstructs a task different from the sender’s intent. It estimates this risk using task-identification probes and uses receiver beliefs to guide message revision and to decide whether additional receiver information is worth acquiring. Experiments on five receivers and six question-answering datasets show improved risk calibration, reductions in probe errors through rewriting, and small gains from selective querying.

Critical strengths

The paper addresses a relevant and rich problem setting, and it clearly distinguishes misunderstanding from inability to execute, making the analysis more insightful and controlled. The problem formulation is sound.

Furthermore, the rewriting results are promising, the ablations are informative, and it helps that the authors pin down that most of the improvement comes from a repair common across receivers rather than from receiver-specific adaptation. To me, this carefulness and transparency increase insight from and confidence in the reported findings.

Critical weaknesses
  1. The interpretation probe is a proxy. To me, selecting a task description from a multiple-choice list only partially reflects the interpretation the model would make during execution (especially in the context of an environment, say e.g., coding). Table 5 strengthens this point, since placing the intended option last increases Nemotron's probe error by roughly 20 percentage points. Although the authors control for position and receiver differences persist, this effect casts doubt on whether this kind of probe faithfully measures interpretation during execution.

    Furthermore, by design, the interpretation probe and actual execution are measured in separate rollouts. This is reasonable to avoid contaminating execution, but it means that probe errors and successful executions cannot establish whether the execution itself involved a misunderstanding. In particular, I am not sure the current evidence can be interpreted as showing that a particular execution can succeed despite a misunderstanding (it can definitely happen, but I am not sure if this is what you show).

  2. It is unclear what each of the receiver-specific components adds specifically. Indeed, receiver-specific recalibration already shows most of the gains. Guidance alone achieves basically the same result as the full method, and replacing the inferred receiver belief with a uniform belief changes only 0.025% of the decisions.

    As mentioned in the strengths, the paper acknowledges this, and a repair that works across receivers is still valuable, although it again makes the practical value of receiver-specific adaptation within the broader framework unclear. Additionally, a natural baseline is missing: instruct the same rewriter to retain the question and explicitly state the required output, using the same intent information and verification but no learned risk model.

  3. The benefit from querying is very modest. The primary-cohort improvement is statistically significant, but corresponds to 0.046 percentage points, and task success does not improve. The replication cohort does not show a statistically significant improvement. Moreover, Experiment 5 uses generic rewrites rather than the guided candidates. Overall, it remains unclear whether querying adds value after the effective shared repair has already been applied, making it unclear how much this component contributes to the results.

Questions for authors
  1. Can you test the interpretation probe by comparing it directly to a behavioral analysis of the actual execution? Given the separate rollouts, can we establish that probe errors reflect the interpretation underlying execution? What assumptions do we need to bridge probe correctness to the risk in (4)?
  2. How does the method compare empirically with the fixed explicit-output rewriting baseline described in the "Weaknesses"?
  3. Does VoII still provide an improvement when applied after guided revision, rather than to generic rewrite candidates?
14 comments
AuthorsOpenReview ↗

Probe validity and the link to actual execution

Thank you for asking how the probe relates to actual execution. Your question helped us add direct behaviour checks.

W1-W2 / Q1: Probe validity and separate calls.

We have added a blinded audit of actual QA outputs and a controlled action test. We report both in Appendix D.4, and Sections 2 and 3 now state the measurement conditions.

W1 / Q1: What the probe measures. Section 2 now defines it as a separate task-identification call. The receiver chooses the intended task, one contrast task, or "None of these/unclear". None records rejection or uncertainty and is stored apart from contrast choices. Both count as probe errors. The resulting rate measures task choices under these options, wordings, and parsing rules. This gives a clear training target for a risk model. Its link to the task inferred during execution needs further assumptions.

W1 / Q1: Direct behaviour check. A blinded Qwen judge labelled archived execution outputs by the task they appeared to attempt, separately from factual correctness. The audit covers 6,629 questions and five receivers: 33,145 pairs, with 31,966 assigned to the intended or contrast task. The table gives contrast-task behaviour in pairs with any probe error minus that in pairs with none. CIs use question-cluster bootstraps.

QA checkDifference (percentage points)
Main1.621
Excluding Qwen1.414
900-question position-balanced0.643

The excluding-Qwen check uses the same judge on the other four receivers. The assigned share is coverage, not judge accuracy. The 900-question interval includes zero.

The controlled action holdout 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. A fixed interpreter records the operation and arguments. 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. We average the Brier difference equally over four task cells fixed before the test.

Action holdoutBrier difference
Probe minus always-intended+0.012743

This favours the simple baseline. These checks support a QA behaviour association and show that probe calibration needs to be tested for each task and protocol.

W1 / Q1: Option position. We agree that Nemotron's position effect matters. Appendix D.3 retains the full result.

Intended-option positionNemotron probe error (%)
Last24.5
First or second3.8

With the intended option first or second, the highest and lowest receiver rates still differ by 3.8 times [3.4, 4.3]. This shows receiver differences under that restriction. Position balancing gives positions equal weight; it does not remove the effect or prove validity during execution.

W2 / Q1: Separate calls and Eq. (4). We agree that a probe error paired with answer success cannot establish the internal task state of that execution. We have changed the result text, figure labels and captions, and table headings. The reported 32% now means the share of soft probe-error weight paired with success in an independent answer call. The conceptual distinction between misunderstanding and execution failure stays useful; the observed pairing has a narrower meaning.

W1-W2 / Q1: Assumptions linking the probe to PIR.

Linking the probe to latent PIR needs valid task descriptions, controlled measurement error, and comparable task interpretations across probe and execution calls. The offered choices must capture the task distinction of interest. The effects of wording, position, rejection, and unparsed replies must also be accounted for. A probe can change how the task is read by showing alternatives. A behavioural judge can also confuse a wrong action with a wrong task. These are part of the measurement problem.

W2 / Q1: The joint relation needed for capability risk.

Eq. (4) conditions action failure on correct interpretation within the same execution. Section 3 now states the required measurement model. It must link the separate probe choices to interpretation and action in that execution. The second head learns answer errors weighted by correct probe responses. Using this head to estimate Eq. (4) requires that joint link.

These changes preserve the useful contribution you highlighted: task identification supplies information that final-answer checks can miss. The revised paper gives that endpoint a precise meaning, tests its relation to behaviour, and states what is needed to use it as an estimate of latent interpretation risk.

AuthorsOpenReview ↗

What receiver-specific modelling adds

Thank you for asking what each receiver-specific part adds. This helps us test prediction, message choice, and query value separately.

The roles of receiver-specific components.

We have made this distinction clearer in Section 6 and Appendix I. Experiments 2, 4, and 5 test these three steps in turn.

Risk prediction. Experiment 2 shows that receiver information mainly corrects risk levels. Recalibrating the receiver-agnostic model separately for each receiver recovers most of the gain.

Gain recovered by recalibrationShare (%)
ECE reduction93
Across-receiver AUROC gain96

The full model adds a small within-receiver ranking gain over that baseline.

Full minus recalibrated baselineDifference
Within-receiver AUROC+0.004
Within-receiver AUPRC+0.007

Appendix I.2 gives the comparison and richer calibration controls.

These are prediction results for the measured probe endpoint. Much of the across-receiver gain reflects receiver risk levels, including Nemotron's position effect. The main text now distinguishes pooled message-receiver ranking from choosing among messages for one receiver. The sender uses risk scores to average loss over receiver types. Whether this changes the best message depends on how candidate messages compare within those types.

Message choice. Experiment 4 shows that shared repair drives most of the gain.

Original Experiment 4 conditionProbe error (%)
Guidance alone2.29
Full method2.31
True identity2.30

These results point to shared repair as the main source of the gain.

The message analysis gives a concrete reason to study a simple rule. For every receiver, the top learned risk feature is an unstated output. Among changed messages sent by the full method, 97% keep the question and add an output line. Most generic rewrites leave that output unstated. This makes a common repair useful before the receiver is known. We have now added the direct fixed-output baseline you suggested; Appendix I.4.1 reports it separately from the original ablations.

The decision counts describe two different checks.

Panel / comparisonMessage outcomeDecisionsShare (%)
Original E4: uniform vs inferred beliefChanged2 / 7,8950.025
Added paired: full vs first valid guidedIdentical7,442 / 7,89594.26

The first check changes the receiver belief; the second adds selection after guided generation. Together with the direct outcome comparisons, they show why gains from these extra steps must be assessed on their own.

Querying. A better belief can identify the receiver more accurately while leaving the selected message unchanged. We have added a direct query-after-guidance test in Appendix I.5.1. Differences are VoII minus no query, in percentage points.

Guided-pool endpointDifference (pp)
Probe error-0.001056
Net utility-0.003808

This directly measures query value after guided revision.

Section 4 explains the relevant condition. Receiver information has decision value when it changes which message has the lowest expected loss. Receivers can have different risk levels while sharing a best message. Under the exact losses in the theorem, a common best message can give zero value from extra receiver information. In the experiments, losses are learned estimates. The theorem gives a clear condition to test with the fitted scores and measured outcomes.

The practical finding is that a system can first apply a shared output repair, then test whether receiver information improves its remaining choices. Our evidence is strongest for receiver-dependent calibration and the shared repair. This keeps the framework's parts clear and gives readers a useful rule for deciding when each part earns its cost.

AuthorsOpenReview ↗

The fixed explicit-output rewrite baseline

Thank you for proposing a simple output rule as a baseline. Your suggestion helped us make the rewrite comparison more direct.

W4 / Q2: The fixed explicit-output baseline.

We have added it in Appendix I.4.1, "Added Fixed Explicit-Output Baseline", and reported its main paired result in the Experiment 4 text. It tests the shared repair identified by the message analysis: keep the question and state the required output. The fixed rule recovers most of the measured rewrite gain.

The rule keeps the full original question word for word and adds one line that states the required output. For example, a request for a designer's name gets a line asking for that name. The rewriter receives the same sender intent and uses four candidates. Candidates use the same semantic-verifier prompt and original validity checks. The baseline receives no receiver identity, receiver belief, learned risk score, or gold answer. It sends the first valid candidate. If all four fail the checks, it sends the original. It does not generate more candidates after rejection or rank candidates with the learned risk model.

The direct comparison covers 1,579 questions, 1,578 question groups, and all five receivers. We measured original, fixed output, guided first valid, and full selection in the same collection. Every distinct message-receiver pair has 36 probes: six wordings by six option orders, with equal weight for each intended-option position. It also has one independent execution call. Identical messages share their measurement. None and unparsed probe replies count as errors under the frozen rule.

W4 / Q2: Paired results and the main comparison.

Probe error in this added panel was:

ConditionProbe error (%)
Original message4.144
Fixed explicit output2.432
First valid guided rewrite2.274
Full method2.300

Paired differences are in percentage points. The full-minus-fixed probe comparison is primary.

Contrast / endpointDifference (pp)
Full - fixed / probe error (primary)-0.132
Full - fixed / probe error (primary)-0.132
Fixed - original / probe error-1.711
Full - fixed / answer failure (secondary)-0.659

Both primary probe intervals include zero. The fixed rule lowers probe error from the original, supporting the practical value of an explicit output line. The secondary answer interval has no correction for multiple tests. The table keeps the main probe result and the secondary answer result separate.

The analysis first averages paired differences over the five receivers within each question. Questions then receive equal weight. The six datasets have different numbers of questions; this is not an equal-dataset average. The original intervals use 10,000 question-ID resamples. The added sensitivity check resamples whole frozen question groups and preserves the same question weights. Both interval sets are shown in the new table.

W4 / Q2: Writer source.

Fixed and guided candidates used the same hosted model name and generation settings. They were generated at different times and through different providers. Most records lack a model fingerprint. We state these source details beside the results. The comparison uses these stored pools and fresh paired receiver measurements collected together for all four conditions.

The new rates are from this fresh measurement, so they differ slightly from the archived Experiment 4 rates. We preserve the original table and label the new panel separately. The full-minus-fixed difference is computed within the new paired panel; it is not formed by subtracting rates from different runs.

This comparison makes the contribution more useful to readers. The learned feature analysis identified a shared repair, and the added baseline shows that a fixed rule can recover much of its measured benefit. The paper presents this rule alongside the paired full-versus-fixed comparison, making its role in message revision clear.

Reviewer_qWBhOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The paper defines prospective interpretation risk (PIR), the probability that a receiver LLM will reconstruct a different task from a message than the sender intended, and measures it with black-box probes kept separate from execution failure. Across several open-weight receivers and question-answering benchmarks, misinterpretation rates differ widely times between receivers, receiver information decreases PIR calibration error, and PIR-guided rewriting lowers interpretation failure, mainly by making messages state the expected output.

Critical strengths
  • The paper focusses on an important problem. (Mis-)communication between agents is a timely and impactful topic.
  • The separation between the interpretation risk and the capability risk is a strong angle. The method is based on a Bayesian-belief principle, which is sound and reasonable for this problem.
Critical weaknesses

Overall, I think this paper is track on becoming a good paper, but it is not ready yet.

  • The paper does not feel ready for publication in its current form. The writing is hard to follow. Sections are not self-contained, for example Section 2 does not introduce properly the notions of the problem (only a careful reading of the introduction gives enough clues). The same is true for Section 3 and 4 (see details below). The paper makes heavy use of notations which blurs the presentation: some are not properly defined, some are confusing (see details below), but their number makes it really difficult to follow even the main arguments of the paper. In some parts, the paper uses overly complicated vocabulary or formulations, which obfuscates the meaning. At least the most related work needs to be folded in the main part of the paper. Overall, the paper is hard to evaluate because it does its ideas and contributions are not clearly explained.
  • Poor experimental settings. The paper advertises it-self as a study of LLM agent communication, but the experimental results are limited to knowledge-based QA benchmarks. These are not representative of how LLM agents operate and how agent would communicate in a multi-agent system.
  • The definition of the posterior of the tasks by the receiver is defined coarsely point-wise on the tasks formulations sampled. This is a strong restriction compared to the wide distribution that the latent task could be. The impact of such restriction is unknown.
Questions for authors

Question

  • Q1. Which assumptions does the approach rely on about the receiver? Since the receiver can be any LLM, it is not clear to me how a posterior can be computed when the receiver is sampled from an unknown distribution.

Details of the presentation issues

References to tables in appendix, and appendices referenced as sections.

Section 2 lacks context to be self-contained and properly introduced the problem of the paper:

  • Line 141: improve the presentation of Y^I and Y^A to clarify interpretation. Especially since Y^I = 0 means correct (which is counterintuitive compared to usual notations in ML).
  • Line 155: the meaning of probe is not introduced here. It needs to be better defined, because this word is used to name different unrelated techniques.
  • Equation 5) defines the soft training target, but no context is given to understand what will be trained and which targets

Section 3 also lacks clarity:

  • heavy wording, hard to parse sometimes. e.g., line 186.
  • definitions at line 188 are hard to understand without defining what are the "receiver-conditioned heads". To what are these heads connected to? How are they trained? What is their purpose?
  • the use of notations is heavy, and this section in particular is hard to follow as a result
  • The notion of “mutable features“ is not defined properly and is unclear what it would mean if the rewrite model is an LLM (the rewrite model is also not properly defined).

Section 4

  • "gold-alias containment": the meaning is unclear (LLM-generated?)
  • "None of these" is not defined. Unclear what it means.
14 comments
AuthorsOpenReview ↗

Response to W1: Clearer writing and main-text guide

Thank you for noting the importance of agent miscommunication and the value of separating interpretation risk from capability risk. Your detailed comments helped us make the setup and method easier to follow. We have made the following changes.

  • Appendix references and language. We corrected the appendix labels. We also used simpler words and shorter sentences.

  • Setup and example. Section 2 now starts with a short example. A question asks for a person's name. Giving a profession changes the task. Giving the wrong name is an execution error. This introduces the two types of error before the symbols.

  • Labels and Eq. (5). Both labels use 1 for failure and 0 for success at the stated stage. A probe is a separate task-identification call. A separate answer call gives an execution label. Eq. (5) averages parsed probe errors for one message-receiver pair. This gives one soft training target for an external predictor. Repeated probes are repeated measurements of that pair. The receiver's weights stay fixed.

  • Receiver-conditioned heads. These are separate supervised predictors. In Experiment 2, each small MLP takes frozen text embeddings and a learned receiver embedding. The interpretation head learns from the soft probe-error target using binary cross-entropy. The second head learns answer-error risk, weighted by the share of correct probe responses. Using this head to estimate capability risk given correct understanding needs a measurement model. This model must link probe choices to interpretation and action in the execution call. Section 3 also describes the models for Experiments 4 and 5. Experiment 4 uses receiver-specific ridge models on changes in eight message features. Experiment 5 fits scorers to measured candidate messages. Appendices F and G.1 give the full model and training details.

  • Mutable features and the rewrite model. "Mutable" means that a wording property can change while the task stays the same. Stating the expected output is one example. The model learns how feature changes are associated with probe-error changes for each receiver. The LLM rewriter, DeepSeek V4 Flash, receives the original message, intended task, context, and editing instructions. It generates four candidates. Fixed checks and a separate semantic-verifier call test whether each candidate keeps the task. The verifier starts with no conversation history and sees neither receiver probabilities nor risk scores. The original message remains an available choice.

  • Gold-alias containment. Section 5 now defines gold-alias containment as a fixed string-matching rule. The scorer normalises the reply and the stored reference answers or aliases. It removes accents, ASCII punctuation, and English articles, uses lower case, and normalises spaces. A match must contain a complete alias with whitespace boundaries. The scoring step uses no LLM and creates no new aliases. Appendix L.2 states that this rule can accept a reply that only mentions the gold answer or miss an unlisted wording.

  • Parsing and training labels. The paper also states how parsing affects the labels. Natural-message tests exclude unparsed probes; Experiment 4 counts them as errors among its 36 probes. These details show how the observed outputs become training targets and message scores.

  • Closest related work. The introduction now ends with a short comparison to the closest listener-aware, clarification, and value-of-information work. This puts the main links to prior work in the main text.

AuthorsOpenReview ↗

Response to Q1: Receiver assumptions and the posterior estimate

Thank you very much for the question.

Receiver assumptions. We have added the receiver assumptions to Section 2 and clarified posterior estimation in Section 3. The unknown quantity is the receiver's identity within a known finite pool. Each type is a frozen model and configuration.

The setting has four main conditions. We can query each known type offline. The receiver used at test time belongs to that pool and keeps its configuration fixed during the interaction. Its history contains actual responses to separate calibration tasks. All types use the same history-sampling rule.

Estimating receiver probabilities. A small history encoder learns from query-response pairs and outputs probabilities over the known types. Training uses receiver-type cross-entropy. A held-out set of histories is used to calibrate the probabilities. An empty history uses a uniform prior. Section 3 now calls the output a calibrated estimate of P(R | history).

Updating the belief and choosing a message. After a new query response, the belief is updated by Bayes' rule:

πt+1ξ,y(r)=P^(y∣R=r,ξ)πt(r)∑r′P^(y∣R=r′,ξ)πt(r′).\pi_{t+1}^{\xi,y}(r)=\frac{\widehat P(y\mid R=r,\xi)\pi_t(r)}{\sum_{r'}\widehat P(y\mid R=r',\xi)\pi_t(r')}.

Here, ξ\xi is the query and yy is its response.

The response probabilities P^\widehat P are estimated from stored responses and smoothed. The Bayes update is computed within this estimated model. The sender then averages the learned losses over all receiver probabilities to choose a message.

Scope. These changes state exactly which probabilities are learned and how they enter the decision. New model families or changed configurations require extending the receiver pool, as now stated in Appendix L.2. The current method supports message decisions when the sender is uncertain about which known receiver it is addressing.

AuthorsOpenReview ↗

Response to W3 and related W1 details: Finite task choices and execution behaviour

Thank you for asking how the offered task choices relate to execution. Your question helped us define the measured risk and check it against visible behaviour.

What the finite task test measures. We revised Section 2 and added Appendix D.4 to explain what the probe measures and how it relates to execution. PIR concerns the task a receiver infers. The probe measures its choice among offered task descriptions. The text now keeps these two objects separate.

W3 and W1 (probe and "None of these"). Each probe presents the intended task, one contrast task, and "None of these/unclear". Different wordings can describe the same task. A choice of None records rejection or uncertainty and is stored separately from a choice of the contrast task. Both count as probe errors. Other possible tasks share this single rejection option, so coverage depends on how the receiver uses the choices.

W3 - Evidence from actual execution. Appendix D.4 reports a blinded Qwen-judge audit of actual QA outputs from 6,629 questions and five receivers. Of 33,145 pairs, 31,966 could be assigned to the intended or contrast task. The difference below is the contrast-task behaviour rate with any probe error minus the rate with no probe error. Values are percentage points (pp).

QA checkBehaviour difference (pp)
Main audit+1.621
Main audit, excluding Qwen+1.414
900-question, position-balanced check+0.643

The judge is an LLM; the share of outputs assigned a label is coverage, not judge accuracy.

W3 - Controlled action check. We also added the controlled action holdout test. It has 48 components and 480 execution units, with 449 assigned to one of the two task operations. Appendix D.4 now gives the task pairs, Brier-score 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. We average Brier differences equally across four task cells fixed before the test.

Score comparisonMean difference (Brier units)
Probe minus always-intended+0.012743

This favours the simple baseline. The paper now reports both the QA association and the calibration gap in this action test.

W3 - Conditions linking probe choices to task risk. Section 3 and Appendix D.4 state the assumptions needed to link the probe to the risk of misunderstanding. These include valid task descriptions, controlled measurement error, and comparable task interpretations across the separate calls. Estimating capability risk given correct understanding needs a measurement model linking probe choices to interpretation and action in the execution call, as stated in Section 3.

Comments on the paper

14 comments
AuthorsOpenReview ↗

Appreciation for the Reviewers’ Feedback and Rebuttal Update

Dear Reviewers and Area Chair,

Thank you for recognizing the novelty and potential of our work and for your thoughtful, constructive feedback. We have now completed our first round of responses to all reviewers and hope that our replies and revisions address your concerns and strengthen confidence to our paper. Your suggestions have been very helpful in improving the paper. The rebuttal has also given us an opportunity to clarify points that were not sufficiently clear in our original submission.

We have uploaded a revised manuscript as a PDF, with additions clearly marked with yellow to make the revisions easier to review. We welcome any further questions or concerns and would be happy to provide additional clarification.

Thank you very much again for your time and careful consideration.

The Authors

AuthorsOpenReview ↗

Clarification on Core Contribution and Supporting Evidence for PIR

Dear Reviewers Area Chair,

We thank you all for recognizing the value of the paper’s central idea, prospective interpretation risk (PIR), and its distinction between task misunderstanding and execution failure. We would like to restate that our contribution is to formalize receiver-dependent interpretation risk before communication and study its implications for message design.

In the rebuttal, we have clarified the formulation, measurement assumptions, and scope, and provided additional analyses and experiments addressing the reviewers’ concerns. In keeping with the emphasis of ICLR’s review guidelines on new knowledge and community value, we hope our clarifications and additional evidence strengthen confidence in PIR’s contribution to understanding LLM based agentic communication.

And we are more than happy to have further communications with you all.

Kind regards,

The Authors

AuthorsOpenReview ↗

Response to your follow-up concerns

Thank you very much for your careful and constructive follow-up. We understand your remaining concerns as four questions:

  1. Does receiver modeling help choose better messages?
  2. Does active querying give a gain after its cost?
  3. A simple rule already gives much of the gain. What does the full method add?
  4. How well does probe risk reflect misunderstanding during actual execution?

We now have complete results for Gemma, GPT-OSS, and Mistral on all 6,629 test questions from six datasets. The runs used our university GPU cluster. GPU queues delayed completion, and these full-test results have just become available. They extend our earlier checks on smaller panels. All new results below use the original candidate and probe prompts, the setting used for the main fixed-rule and query comparisons in the full-test plan.

The results in Questions 1-3 use the same full-test panel of 19,887 question-receiver pairs. We give equal weight to the three receivers. We first average their results for each question, then average over questions. Each distinct sent message has 36 balanced probes. Rates are percentages. Gains, costs, and their intervals are in percentage points.

Please refer to the following comments.

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

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