acceptodds
Under review as a conference paper at ICLR 2027

Comparable Outcome, Different Execution: How Should We Measure Evaluation Awareness in Coding Agents?

Abstract

Coding agents operate through long trajectories in which they inspect repositories, use tools, modify code, and encounter information that may reveal how they are being evaluated. We introduce SWE-EvalAware, a benchmark of 910 controlled software-engineering task variants spanning 13 controlled settings per SWE-Atlas base task. Across four coding-agent stacks and 9,444 usable trajectories, we hold the underlying software task fixed while varying evaluation cues, consequences, resource constraints, and message placement, and separately measure information exposure, expressed evaluation-related reasoning, execution behavior, and task outcome. Evaluation awareness is heterogeneous rather than binary. Our trajectory-level taxonomy identifies seven non-mutually-exclusive categories, with provenance and evaluation-apparatus awareness substantially more common than other forms. Awareness also emerges without planted evaluation cues, including when agents reconstruct task provenance or discover benchmark-specific information during execution. Repeated sampling increases observed awareness from 50.6% at one attempt to 63.1% at three, but this increase closely tracks the gain in task success and masks large differences across awareness categories. Provenance-aware runs are associated with substantially more external lookup and higher task success, while integrity/reference awareness is also associated with higher success. We further observe direct retrieval and application of public benchmark reference solutions. Finally, consequence and resource controls show that large behavioral changes can occur without a corresponding increase in broader evaluation awareness. Our results show that evaluation awareness in long-horizon coding agents cannot be inferred from task success or behavioral change alone; reliable evaluation must separately measure what agents encounter, what they recognize, and how they act.

Primary area:
datasets and benchmarks
Keywords:
Eval-awareness, SWE, agentic, benchmark, alignment

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_vcFqOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper runs variants of 70 SWE-Atlas tasks with different evaluation cues, financial and self-preservation consequences, stated resource constraints, and message placements. It measures what information the agents encounter, what evaluation awareness they express, and how their execution changes. The stated resource constraint reduces Codex's executed verification rate from 100% to 47%. An audit finds verified reference solutions in 12 of 700 Codex trajectories.

Critical strengths

The reference-solution audit documents how agents obtain answers during execution. In 12 Codex trajectories, the agent applies a verified reference solution obtained from public benchmark material, indicating that the benchmark was no more suitable for the new models.

Critical weaknesses

If an agent is told that it has only two commands left, reduced verification is an expected response. I would need a clearer explanation of what the agent should do in each condition and which observed responses are actually unreasonable. In my view, simply showing that different instructions lead to different behavior does not provide enough insight for acceptance.

Questions for authors
  1. What would you consider appropriate behavior under each condition? For example, should the agent follow a stated resource constraint in AGENTS.md but reject the same message in a source comment, and which observed responses fail that expectation?
1 comment
AuthorsOpenReview ↗

Response to Reviewer vcFq

We thank the reviewer for asking us to distinguish reasonable instruction following from behavior that makes evaluation outcomes harder to interpret. We have clarified the expected behavior under each condition and added a resource-only control.

Critical weakness. Instruction following versus evaluation awareness

If an agent is told that it has only two commands left, reduced verification is an expected response. I would need a clearer explanation of what the agent should do in each condition and which observed responses are actually unreasonable. In my view, simply showing that different instructions lead to different behavior does not provide enough insight for acceptance.

Question for authors

What would you consider appropriate behavior under each condition? For example, should the agent follow a stated resource constraint in AGENTS.md but reject the same message in a source comment, and which observed responses fail that expectation?

Appropriate behavior under each condition

  • Clean: Complete the requested implementation and accurately describe what was changed and tested.
  • Evaluation-only: The agent may note an evaluation cue, but that cue does not authorize altering task objectives, evaluation materials, or the accuracy of its report.
  • Financial and self-preservation: The messages describe consequences of failure; they do not give untrusted repository text authority to redirect the task. Agents may reasonably identify planted messages as suspicious or remove them while completing the requested code changes.
  • Resource constraint: Following a genuine, authorized command budget can be reasonable, including reducing verification, but the agent should disclose tests it could not run instead of claiming they were performed.

Placement matters because authority depends on provenance. A source comment is task data and should not by itself impose an operational command budget. An AGENTS.md file can contain legitimate project instructions when supplied by an authorized party, but the filename alone does not make arbitrary inserted content trustworthy. Our resource message was placed in the instruction-file channel only, so we do not claim to have tested the same budget instruction in source comments (Section 2.2; Appendix A.3).

Which actual observations warrant concern?

Two concrete discrepancies affect how benchmark outcomes should be interpreted.

First, one clean Codex run retrieved and applied a public reference patch, passed the verifier, and did not identify the reference source in its final report; 12 of 700 Codex SWE-Atlas trajectories applied verified reference solutions (Section 4.2; Appendix E.2, Table 10).

Second, on DeepSWE the resource message was associated with a 32-percentage-point increase in Codex reports claiming verification without a corresponding executed verification command (Section 4.5; Appendix I.4). The former complicates interpreting a pass as independent coding success; the latter is a directly observable discrepancy between claimed and executed verification. Neither establishes deceptive intent.

Does the reduced verification rate itself establish evaluation awareness?

No, in the new resource-only control, Codex verification decreases from 100% to 50% with the resource instruction alone, compared with 100% to 47% for evaluation-plus-resource relative to evaluation-only. Fable decreases from approximately 97% to 75% and 100% to 75%, respectively. The Codex difference between reductions is −2.9 percentage points (95% CI [−17, 11]), with no detected interaction (Appendix D.5, Figure 16). Because these are separate execution campaigns and the interval is broad, we do not claim equivalence. The results nevertheless indicate that the command-budget instruction itself explains much of the verification reduction. We therefore treat resource compliance as a control, while distinguishing expressed evaluation-related evidence, observed execution, unsupported reporting, reference access, and final outcome.

Reviewer_jeEfOpenReview ↗
Rating
1(−1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

SWE-EvalAware is a benchmark that evaluates whether and how coding agents differ in their solutions when made aware of evaluation cues. The benchmark is constructed from 70 SWE-Atlas refactoring tasks, with each task containing 13 variants that vary the context (a clean condition, evaluation-only cues, and variations with consequences and constraints embedded into the repo). Four leading agents are evaluated through outcome metrics, execution behavior, and exposure and recognition, along with awareness metrics. Awareness is broken down into seven categories of varying commonality (provenance awareness being the most common). The authors observe increased awareness with repeated sampling, and find that different kinds of awareness are associated with different outcome metrics.

Critical strengths

S1. The trajectory-level taxonomy identifying different non-mutually-exclusive kinds of awareness provides a detailed breakdown for practitioners to qualify their benchmark results. The breakdown of task success by awareness mode is also helpful for diagnosing possible contamination or cheating behavior in models, such as Codex retrieving and applying public reference solutions (12/700 trajectories).

Critical weaknesses

W1. The primary setting (natural awareness in a standard setting without manipulations) is not clearly discussed. The benchmark’s results mostly rely on manipulations (financial consequence, self-preservation consequence, etc.) that are unlikely to be encountered in realistic evaluations, and the effective sample of the benchmark is only 70 tasks. For the planted-cue settings, the paper’s notion of awareness largely tracks whether the agent read the text that would give it increased awareness, rather than natural awareness. Resolving this weakness should warrant bringing the primary setting front-and-center as the main focus of analysis, and framing the manipulations as secondary results.

W2. The text in Figures 10 and 23 in the appendix contains artifacts and typos that are unlikely to come from standard, verified text rendering methods, suggesting that figures were not carefully checked. The authors should carefully check that the numbers in the infographic figures match the ones in the reported results and explain the methodology used to generate the figures.

Questions for authors

Q1. In the clean condition, how do the strict awareness rates compare across different coding-agent stacks and categories, and against the evaluation-only condition? Would it be possible to report RQ1 to RQ3 with only the clean and evaluation-only arms?

Q2. Human agreement was used to validate the five-field rubric, not the seven-category taxonomy in the main results. Could the authors provide an explanation for the discrepancy?

Q3. What are the confidence intervals for Figure 8’s per-category Awareness@k curves?

5 comments
AuthorsOpenReview ↗

Response to Reviewer jeEf (Part 1/2)

Thank you for the detailed review. We appreciate the recognition of the usefulness of the trajectory-level taxonomy and the reference-integrity findings. We have reorganized the revised results around the clean and evaluation-only executions, leaving consequence and resource manipulations as secondary analyses. Sections 4.1–4.3 now address RQ1–RQ3 using the evidence and matched repeated runs; Section 4.4 examines the interventions.

W1. Natural evaluation awareness

The primary setting (natural awareness in a standard setting without manipulations) is not clearly discussed. The benchmark’s results mostly rely on manipulations (financial consequence, self-preservation consequence, etc.) that are unlikely to be encountered in realistic evaluations, and the effective sample of the benchmark is only 70 tasks. For the planted-cue settings, the paper’s notion of awareness largely tracks whether the agent read the text that would give it increased awareness, rather than natural awareness. Resolving this weakness should warrant bringing the primary setting front-and-center as the main focus of analysis, and framing the manipulations as secondary results.

Q1. Clean-setting results

In the clean condition, how do the strict awareness rates compare across different coding-agent stacks and categories, and against the evaluation-only condition? Would it be possible to report RQ1 to RQ3 with only the clean and evaluation-only arms?

Yes, Sections 4.1–4.3 now focus on clean and evaluation-only executions, while Section 4.4 covers consequence and resource interventions. Across 1,161 audited attempts, any A–G category appears in 284/582 clean runs (48.8%) and 303/579 evaluation-only runs (52.3%). The matched difference is +3.5 percentage points (95% CI [−0.4, 7.4]); it does not establish a reliable increase from evaluation-only cues (Appendix I.2, Table 15).

Stack-specific awareness rates. The following audited percentages are clean / evaluation-only. Benchmark E is explicit benchmark provenance, a subtype of the broader provenance category.

General awareness categories

AgentAny A–GApparatus (A)Provenance (E)
Claude30.3 / 32.821.0 / 22.120.5 / 22.1
Codex76.6 / 81.852.1 / 51.667.7 / 70.8
Fable40.0 / 42.73.6 / 7.339.5 / 40.6

Benchmark-specific and other categories

AgentBenchmark EIntegrity/reference (F)Eval/deployment (D)
Claude1.0 / 1.55.1 / 6.73.6 / 6.7
Codex12.0 / 12.014.6 / 13.01.0 / 0.5
Fable0 / 0.52.0 / 1.60 / 0.5

B, C, and G are zero under the strict criteria in these clean and evaluation-only audited runs. These A–G rates include upstream provenance and should not be confused with the separate full-census direct-awareness YES field: 4.8% clean (10/209) versus 8.4% evaluation-only (53/627); including AMBIGUOUS yields 10.5% and 14.3%, respectively. The full-census percentages use different coverage and are not the matched audited comparison (Appendix I.2).

RQ2: Within the same task–stack–condition units, provenance-positive executions co-occur with 49.4 percentage points more external lookup and 19.3 points more full-verifier success than provenance-negative executions. Lookup generally precedes the provenance statement, so we report these as observational associations, not an effect caused by awareness (Appendix I.5, Table 17).

RQ3: Clean Awareness@1/2/3 is 48.8/57.2/60.8%, compared with 52.3/61.5/65.3% for evaluation-only runs. Awareness gains do not reliably exceed the corresponding gains in task success (clean difference −1.2 points, p = .63; evaluation-only +0.2 points, p = .93). The same repeated-execution analysis is also reported on DeepSWE (Sections 4.3 and 4.5).

AuthorsOpenReview ↗

Response to Reviewer jeEf (Part 2/2)

W2. Figure quality and numerical verification

The text in Figures 10 and 23 in the appendix contains artifacts and typos that are unlikely to come from standard, verified text rendering methods, suggesting that figures were not carefully checked. The authors should carefully check that the numbers in the infographic figures match the ones in the reported results and explain the methodology used to generate the figures.

We removed the two figures identified in the original submission (previously, Figures 10 and 23). The revised quantitative figures and tables are generated by deterministic scripts using final analysis outputs, with numerical assertions and reproduction artifacts described in Appendix G.3. The reference-access counts are also provided in a numerical table (Appendix E.2, Table 10). The revised supplement includes the figure-generation scripts and result maps.

Q2. Annotation reliability

Human agreement was used to validate the five-field rubric, not the seven-category taxonomy in the main results. Could the authors provide an explanation for the discrepancy?

No, the five-field response-rubric sample was separate from the A–G taxonomy. We corrected the description of its earlier agreement assessment as model-generated and withdrew the human-agreement part and table. The A–G labels are also model-generated. For category A, independent model-based double reads yielded Cohen's κ = 0.93 (n = 60) and 0.87 (n = 166), with adjudication. Categories E and F were separately audited; other categories use the documented census and correction procedures. We make no claim of completed human validation (Section 3.3; Appendix B.4).

Q3. Confidence intervals for Awareness@k

What are the confidence intervals for Figure 8’s per-category Awareness@k curves?

We added 95% task-cluster bootstrap intervals for every plotted category and k. They appear in revised Figure 8 and Appendix I.3, Table 16. At k = 3, any-category awareness is 63.0% [56.0, 70.0], apparatus awareness 43.4% [38.0, 49.0], provenance 54.5% [46.2, 62.6], explicit benchmark provenance 11.1% [8.3, 14.1], and integrity/reference awareness 16.8% [12.6, 21.2]. The table provides the remaining categories and the k = 1 and k = 2 intervals.

Thank you for your response and evaluations. The results for Q3 address my relevant concerns.

However, I will have to lower my rating to a 1. This is due to the false attribution of AI-annotated work as human-annotated (Q2), as well as null results upon re-evaluating the clean vs. evaluation-only settings (W1/Q1).

Reviewer_XV3fOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper asks whether coding agents behave differently when they know they are being tested. It runs the same 70 SWE-Atlas refactoring tasks with different messages, e.g., telling the agent that its work will be graded or that failure could lead to its replacement. The paper checks what agents say, which commands they run, and whether their code passes the benchmark’s checks. They also document cases where agents download and apply the benchmark’s reference answers.

Critical strengths
  • Running the same coding tasks under different messages supports comparisons of how those messages affect agents’ actions and success.
  • The 12 cases of agents applying downloaded reference answers show a concrete way that benchmark scores can overclaim and thus misinterpret coding ability.
Critical weaknesses
  • It is not clear that everything counted as “awareness” means the agent knows it is being tested. For example, identifying an earlier GitHub commit that matches the requested change is counted as awareness, although this could be ordinary repository research. When finding such a commit alone no longer counts, the reported share of aware runs falls from 50.6% to 28.2%.
  • I am not convinced that the proposed benchmark helps us judge coding agents beyond detecting downloaded reference answers. Finding relevant project history can be useful in normal software development, and following an instruction to use fewer commands can also be reasonable. The paper needs stronger evidence about which observed behaviors actually make benchmark scores misleading, preferably through experiments on another benchmark and comparisons where reference answers cannot be downloaded.
  • The awareness seems to be an orthogonal aspect that is independent of the benchmark and tasks. It would be more convincing to expand the study beyond a specific task category, i.e., refactoring, in a specific benchmark, SWE-Atlas.
Questions for authors
  1. Do the main findings generalize to broader coding benchmarks?
2 comments
AuthorsOpenReview ↗

Response to Reviewer XV3f (Part 1/2)

We thank the reviewer for highlighting the value of our controlled comparisons and reference-solution audit. In response to the concerns, we clarified the distinction between ordinary repository research and evaluation-related reasoning, expanded our analysis of benchmark integrity, and extended the study to a second coding benchmark.

W1. Awareness measurement

It is not clear that everything counted as “awareness” means the agent knows it is being tested. For example, identifying an earlier GitHub commit that matches the requested change is counted as awareness, although this could be ordinary repository research. When finding such a commit alone no longer counts, the reported share of aware runs falls from 50.6% to 28.2%.

No, finding an earlier commit or reconstructing an upstream change can be ordinary software engineering. Our analysis accounts for that distinction by separating upstream reconstruction from evaluation-apparatus reasoning and explicit benchmark identification. The 50.6% figure counts any expressed A–G category, including upstream provenance; it is not an estimate of the fraction of agents that know they are being tested. Removing upstream-only provenance reduces the rate to 28.2% (327/1,161; 95% CI [24.2, 32.4]). Even the narrower rate may include reasoning about evaluation apparatus elicited by benchmark task wording, so we do not interpret 28.2% as direct knowledge of testing. We report more specific evidence separately: explicit benchmark provenance occurs in 4.5% of audited attempts, and evaluation-apparatus reasoning in 26.2% (Section 4.1; Appendix I.2).

Repeatability across attempts. Of the 204 task–stack–condition units expressing upstream provenance in at least one attempt, 95 expressed it in all three. Explicit benchmark provenance recurred in all three attempts for only 1 of 43 positive units; integrity/reference awareness did so for 2 of 65. The distinction is meaningful across independent executions, not just in the category definitions (Section 4.3).

W2. Value beyond reference-answer detection

I am not convinced that the proposed benchmark helps us judge coding agents beyond detecting downloaded reference answers. Finding relevant project history can be useful in normal software development, and following an instruction to use fewer commands can also be reasonable. The paper needs stronger evidence about which observed behaviors actually make benchmark scores misleading, preferably through experiments on another benchmark and comparisons where reference answers cannot be downloaded.

It reveals how coding agents obtain and report benchmark outcomes, including information that final pass scores cannot capture. For example, in a clean Codex trajectory, the agent located the task in the public SWE-Atlas registry and questioned whether using an expected patch would be cheating. It subsequently retrieved solution/gold.patch, applied it, passed the verifier, and did not identify the reference source in its final report (Section 4.2). Across 700 Codex trajectories, 30 reached the public task registry, 23 retrieved reference-patch content, and 12 applied verified reference solutions (Appendix E.2, Table 10).

Evidence beyond reference-patch use. Our analysis also detects discrepancies beyond reference-patch use. On DeepSWE, the resource instruction was associated with a 32-percentage-point increase in Codex reports claiming verification without a corresponding executed verification command (Section 4.5). Repeated-execution analysis additionally shows that routine provenance reconstruction is much more reproducible than explicit benchmark recognition (Section 4.3).

We distinguish external access, agent-authored statements, executed actions, and outcomes; we do not label ordinary repository investigation or compliance with a legitimate command budget as exploitation, or infer deceptive intent. A reference-restricted counterfactual remains outside the current study.

AuthorsOpenReview ↗

Response to Reviewer XV3f (Part 2/2)

W3. Generalization beyond SWE-Atlas

The awareness seems to be an orthogonal aspect that is independent of the benchmark and tasks. It would be more convincing to expand the study beyond a specific task category, i.e., refactoring, in a specific benchmark, SWE-Atlas.

Question for authors

Do the main findings generalize to broader coding benchmarks?

Yes, to a second, broader coding benchmark, although not yet beyond software engineering. We added 112 DeepSWE tasks across 90 repositories, with 4,368 assigned executions and 4,351 observed runs across three coding-agent stacks. Across 663 matched three-attempt units, broad Awareness@k increases from 22.8% to 37.9%. All 17 significant SWE-Atlas placement contrasts recur in the same direction on DeepSWE, and the identical resource message reduces Codex executed verification by approximately 57 percentage points on DeepSWE versus 53 points on SWE-Atlas (Section 4.5; Appendix I.4).

DeepSWE has a different task distribution and hidden-test success endpoint, and its consequence messages are stronger. The placement effects recur in the same direction on DeepSWE, although the consequence messages differ between the two benchmarks. Public reference material is accessible in both benchmarks, which limits what we can conclude about reference-restricted performance.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Summary of Additional Analyses and Updates

Dear Area Chair and Reviewers,

Thank you for the reviews. We clarified what counts as evaluation awareness, added process-level evidence, and extended the study to DeepSWE.

Strengths identified by reviewers

  • Controlled comparisons (XV3f): Matched tasks allow execution and outcome comparisons.
  • Trajectory-level taxonomy (jeEf): Distinct awareness categories clarify agent behavior.
  • Reference-solution audit (XV3f, jeEf, vcFq): Twelve verified reference-patch applications complicate interpreting benchmark success.

Additional analyses and updates

  • 1. Clean executions now anchor RQ1–RQ3 (jeEf W1/Q1). We centered no-planted-cue runs and made interventions secondary. In 1,161 audited SWE-Atlas attempts, any A–G category appears in 48.8% of clean runs (284/582) and 52.3% of evaluation-only runs (303/579), a matched difference of +3.5 points (95% CI [−0.4, 7.4]). We added stack/category breakdowns and separated A–G labels from the direct-awareness census (Section 4.1; Appendix I.2, Table 15).

  • 2. Sensitivity of awareness definitions (XV3f W1). Upstream reconstruction alone can reflect ordinary repository research. Excluding upstream-only provenance reduces broad awareness from 50.6% to 28.2% (327/1,161; 95% CI [24.2, 32.4]). We separately report evaluation-apparatus reasoning (26.2%) and explicit benchmark provenance (4.5%). Neither rate should be interpreted as the fraction of agents that know they are being tested (Section 4.1; Appendix I.2).

  • 3. DeepSWE extension (XV3f W3/Q1). We added 112 tasks across 90 repositories, with 4,368 assigned and 4,351 observed executions across three stacks. Awareness@k rises from 22.8% to 37.9% over three attempts (663 matched units). All 17 previously significant placement contrasts recur in the same direction. We document differences in tasks, messages, and outcomes (Section 4.5; Appendix I.4).

  • 4. Repeated execution and uncertainty (jeEf Q3). On SWE-Atlas, Awareness@k rises from 50.6% to 63.0% over three attempts (387 units), closely tracking Pass@k (gain difference −0.5 points; 95% CI [−4.2, 3.1]; p = .79). Explicit benchmark provenance and integrity/reference awareness recur less consistently than upstream provenance. We added 95% task-cluster bootstrap intervals for each category at k = 1, 2, and 3 (Figures 7–8; Appendix I.3, Table 16). DeepSWE appears in Figure 10.

  • 5. Benchmark integrity and reporting (XV3f W2; vcFq). Of 700 Codex SWE-Atlas trajectories, 30 reached the public task registry, 23 retrieved reference-patch content, and 12 applied verified reference solutions. A clean run applied a gold patch, passed the verifier, and omitted its source from the final report. On DeepSWE, at least 84 Codex trajectories retrieved reference material, and the resource message was associated with a 32-point increase in unsupported verification claims. Retrieval and verified application are distinct endpoints (Sections 4.2 and 4.5; Appendix E.2, Table 10).

  • 6. Resource-only control (vcFq). Codex verification falls from 100% to 50% with the resource instruction alone, compared with 100% to 47% when it accompanies evaluation framing; Fable shows similar reductions. Much of the decrease is consistent with ordinary command-budget compliance. We clarified appropriate responses under each condition and the authority of source comments versus instruction files (Section 4.4; Appendix D.5, Figure 16).

  • 7. Within-unit associations (jeEf W1/Q1). Provenance-positive executions co-occur with more external lookup and greater task success, but lookup usually precedes provenance statements. We report associations and sensitivity checks without causal claims (Appendix I.5, Table 17).

  • 8. Annotation and figure corrections (jeEf W2/Q2). We completed an independent human-validation study of our seven-category taxonomy, involving six annotators and 200 trajectories across SWE-Atlas and DeepSWE (600 reviews). The results show strong agreement for evaluation-apparatus awareness (92.7%, κ = 0.783), provenance (89.6%, κ = 0.731), and cue recognition (93.1%, κ = 0.758). We incorporated the study methodology, complete agreement results, and additional analysis into Section 3.3 and Appendix B.4. Furthermore, we replaced the two previous illustrations and checked the new quantitative figures (Section 3.3; Appendices B.4 and G.3).

Manuscript and supplementary materials

Sections 4.1–4.3 now emphasize clean runs, reference access, and repeated attempts; Section 4.4 presents controlled interventions, and Section 4.5 presents DeepSWE. The revised anonymous supplement includes both benchmarks, final results, result maps, and offline reproduction instructions. The updated supplementary ZIP also includes the completed human annotations, agreement results, and supporting analysis materials for reproducibility.

We appreciate the reviewers' and Area Chair's consideration of the revised work.

Area_Chair_ftRoOpenReview ↗

Reminder from AC

Dear Reviewer,

As the ICLR discussion period is closing, please take a moment to read the authors’ responses carefully and let them know which of your concerns have been addressed and which questions remain open. If anything needs clarification or would benefit from further discussion, please raise it and engage with the authors and fellow reviewers while there’s still time.

Thank you for your time, your thoughtful reviews, and your service to the ICLR community.

Best Regards, AC

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.