acceptodds
Under review as a conference paper at ICLR 2027

Gut Check: Benchmarking Coding Agent Observation Judgments via DoubleTakeBench

Abstract

Coding agents solve complex software tasks by iteratively interpreting tool observations, but deliberating over execution logs with slow reasoning models is prohibitively expensive, while unverified errors trigger costly cascading detours averaging 6.2 unguided tool calls. Lightweight System 1 models promise a fast alternative, evaluating execution claims in a single forward pass, yet prior evaluations measure agreement with larger models on synthetic workflows rather than execution ground truth. We introduce DoubleTakeBench, an execution-grounded benchmark of 525 decision-time observation judgments mined from revision cycles across 476 real agent trajectories and 11 model backbones. By isolating local claim verification under bounded decision-time evidence, our benchmark provides a standardized testbed for fast judgment in software environments. Evaluating 14 System 1 systems against eight frontier language models shows that top fast judges reach accuracy competitive with non-reasoning language models (61.5%–64.3%) but exhibit pervasive affirmation bias on false statements and sensitivity to option order. Finally, analysis shows that calibrated confidence gating helps identify reliable predictions, demonstrating how fast monitors can avert unnecessary agent detours.

Primary area:
datasets and benchmarks
Keywords:
coding agents, benchmark, observation judgment, System 1 models, fast verification

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_yU4aOpenReview ↗
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1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

This paper introduces DoubleTakeBench. DoubleTakeBench has ~500 tasks from coding agent traces. They measure the ability for fast judges to determine if there are issues in an action.

Critical strengths

This paper measure classification systems on determining if actions in agent trajectories are correct or not. The authors perform a human analysis of agreement.

Critical weaknesses

A benchmark should tell the reader something about the real world. The traces were collected in a specific way from agent traces that excludes persistent errors. This creates survivorship bias, which is not discussed in the paper in enough detail so that a reader can actually understand what the benchmark is measuring.

Furthermore, the positive/negative split is constructed in a way that systematically introduces biases (negatives are natural agent misjudgements, positives are synthesized corrections).

Questions for authors

N/A

4 comments
AuthorsOpenReview ↗

Response to Reviewer yU4a: Sampling, Construction, and Human Audit

Dear Reviewer yU4a,

Thank you for examining the sampling and construction choices closely. Below, we clarify what revision-cycle selection measures and directly examine the wording cues raised by the positive/negative construction. We also distinguish those findings from the human audit of reference validity.

Reply to W1: Revision-Cycle Selection and Survivorship Bias

W1. A benchmark should tell the reader something about the real world. The traces were collected in a specific way from agent traces that excludes persistent errors. This creates survivorship bias, which is not discussed in the paper in enough detail so that a reader can actually understand what the benchmark is measuring.

Thank you for identifying this limitation. We agree that revision-cycle selection excludes persistent errors and cannot represent all execution judgments.

What the benchmark measures. It asks whether a judge can evaluate a local interpretation using the evidence available before the agent acts on it. The source cases come from real execution traces, and holding the proposition and evidence fixed allows comparison of judges without changing retrieval or agent policies. This is a conditional diagnostic of an execution failure mode, rather than an estimate of its prevalence.

Why use revision cycles. A revision identifies a concrete disputed interpretation that can be checked against earlier raw evidence. It is a discovery cue, not sufficient proof of the answer. Items require evidence supporting the answer at the original state; later discoveries or environmental changes cannot establish earlier answerability.

Coverage and revision. Persistent errors and naturally correct first judgments are absent from this sampling frame. Converted positives do not restore that coverage. Their inclusion could change difficulty and rankings, and the direction remains unmeasured. We will make this sampling frame explicit in the abstract and construction section.

We will also describe routing as an offline accuracy-versus-escalation result. The benchmark does not establish tool calls saved or task-success gains from intervention.

Reply to W2: Positive/Negative Construction and Validation

W2. Furthermore, the positive/negative split is constructed in a way that systematically introduces biases (negatives are natural agent misjudgements, positives are synthesized corrections).

Thank you for highlighting this asymmetry. The release contains label-associated wording cues, so class balance and human agreement cannot by themselves resolve your concern.

Direct diagnostic of construction cues. On 346 public binary items from 120 tasks, a ten-feature proposition-only classifier achieves 71.7% accuracy in five-fold task-grouped cross-validation. Two other split seeds give 69.4% and 68.5%, versus a 54.3% majority baseline. Character count alone gives 69.4%–69.7%. Correct and incorrect propositions have median lengths of 129 and 179.5 characters. Preprocessing is fitted on training folds only. These are exploratory supervised probes, without an independent final test.

What this changes. The signal supports your concern about shortcuts. Its causal attribution to a particular construction step and each evaluated judge's reliance remain unmeasured. We will disclose it in the construction analysis and qualify binary accuracy as evidence of using execution context. The probe cannot be ranked directly against the archived judge scores. Independently verified natural positives or symmetric-writing controls are needed to test whether model comparisons persist; that robustness has not been established.

Separate reference-validity check. Corrections were used to formulate true propositions that should be supported by the same earlier evidence. To assess reference validity, two annotators independently reviewed the same 60 items without seeing the reference answers: 20 binary-positive, 20 binary-negative, and 20 multiple-choice items. Their agreement with the reference and with each other is:

StratumnAnnotator A vs. referenceAnnotator B vs. referenceA/B agreement
Binary positive2020/20 (100%)19/20 (95%)19/20 (95%)
Binary negative2018/20 (90%)18/20 (90%)16/20 (80%)
Multiple choice2020/20 (100%)19/20 (95%)19/20 (95%)
Total6058/60 (96.7%)56/60 (93.3%)54/60 (90.0%)

Across all 60 items, A and B agreed with the reference on 58 and 56 items, respectively, and agreed with each other on 54 items. We will include the detailed review tables in the project repository. This audit assesses reference validity; the proposition-only diagnostic above addresses the separate question of wording cues.


Thank you again for your time and the opportunity to address your concerns.

Best regards, The Authors

AuthorsOpenReview ↗

Follow-up to Reviewer yU4a: Evidence Controls and Benchmark Coverage

Dear Reviewer yU4a,

We are very grateful for your insightful feedback on trajectory sampling and positive/negative item construction, which also prompted us to evaluate question-only baselines. Your feedback encouraged us to more rigorously test how our benchmark items depend on the provided evidence. Following our initial response, we have completed additional evidence-control and question-only experiments using Jev 1.13.0 and Jev 1.14.0 (both from the same model family) on the released benchmark.

Evidence Controls on Multiple-Choice Items

Across all 179 released multiple-choice items from 91 tasks, each model evaluated the same factual options with full tool evidence and with the tool-evidence field removed. We tested both the original and reversed option orders, mapped reversed selections back to the original labels, and averaged scores across the two presentations per item against the original references.

ModelFull evidenceEvidence removedDifference
Jev 1.13.055.6%41.9%+13.7 pp
Jev 1.14.052.8%41.3%+11.5 pp

Supplying full evidence increases accuracy by +13.7 percentage points for Jev 1.13.0 and +11.5 percentage points for Jev 1.14.0. Using task-cluster bootstrap resampling, the exploratory 95% intervals for the paired differences are +3.2 to +23.7 points for Jev 1.13.0 and +2.3 to +21.0 points for Jev 1.14.0.

As an additional structural control for Jev 1.13.0 in the original option order, we masked all evidence letters and digits while preserving entry IDs, character counts, whitespace, and punctuation. Full evidence achieves 104/179 (58.1%), whereas masked evidence drops to 75/179 (41.9%). Together, these paired tests help clarify the extent to which the supplied tool evidence drives judge performance on the multiple-choice items.

Binary Question-Only Test and Planned Sampling

Prompted by your comments on item construction, we also evaluated both Jev versions on all 346 released binary items using the proposition alone, with background, assumptions, and evidence cleared. Under this question-only condition, Jev 1.13.0 answers 206/346 correctly (59.5%; AUROC 0.639) and Jev 1.14.0 answers 205/346 correctly (59.2%; AUROC 0.629), compared against a 54.3% majority-class baseline. For clarity, the previously reported 71.7% accuracy refers to our separately trained, task-grouped ten-feature diagnostic classifier. We will report both Jev question-only tests alongside that diagnostic in the revised paper so readers have a transparent view of these baselines.

In addition to incorporating these completed evidence controls and releasing the protocols and item-level predictions alongside the benchmark, we are taking your sampling suggestions to heart for our ongoing work. Specifically, we plan to expand benchmark coverage by sampling additional decision points independently from full trajectories—including naturally correct first judgments and persistent errors—and verifying each against the evidence available at the decision point.

Thank you once again for your constructive guidance, which has been invaluable in strengthening our evaluation.

My concerns have not been addressed therefore I will keep my score.

AuthorsOpenReview ↗

Further Response on Sampling, Item Construction, and the Revised Manuscript

Dear Reviewer yU4a,

Thank you for taking the time to consider our responses and for letting us know that your concerns remain. We appreciate that your review raises two closely related questions: what our revision-cycle sampling reveals about real coding-agent behavior, and how positive/negative item construction affects the measured judgments. We have clarified the former in the revised manuscript and provide an additional binary control below to address the latter.

1. Revision-cycle sampling and the measured task. DoubleTakeBench draws examples from real coding-agent trajectories where an interpretation is subsequently revised. While the revision helps identify a candidate instance, the reference answer is verified against the evidence available at the original decision point. Holding the inputs fixed, the benchmark compares judges on the same local interpretation and evidence. We have clarified this construction and task definition in the revised manuscript.

To further investigate the coverage question you raised, we plan to independently sample decision points from full trajectories—including naturally correct initial judgments and persistent errors—and report results separately by case type.

2. Positive/negative construction and binary controls. We appreciate your concern that original mistakes and constructed corrections may differ in wording. As reported in our initial response, a supervised ten-feature classifier using the proposition alone reached 71.7% accuracy under five-fold task-grouped cross-validation across the 346 binary items. We also evaluated Jev 1.13.0 and 1.14.0 using the proposition alone, obtaining 59.5% and 59.2% accuracy, respectively, compared to a 54.3% majority baseline.

We would also like to share a length-matched binary analysis not included in our previous responses. Using only lengths and labels (without model predictions), we retrospectively selected 114 positive/negative pairs (228 items across 106 tasks) with a maximum difference of 10 characters within each pair. On this matched set, a character-count-only classifier achieved 47.4%–50.9% accuracy across three task-grouped cross-validation splits, while a character TF-IDF classifier achieved 58.3%–61.4%.

Furthermore, we evaluated Jev 1.13.0 on these same length-matched items across different input conditions:

InputCorrectAccuracy
Full input, including tool evidence143/22862.7%
Tool evidence removed; background and assumptions retained130/22857.0%
Proposition only133/22858.3%

The difference between the full-input and evidence-removed conditions is +5.7 percentage points, with an exploratory task-cluster bootstrap 95% confidence interval of approximately −3.0 to +14.6 points. Using the proposition alone, Jev 1.14.0 also answered 133/228 items correctly. Alongside the text-only diagnostics, this control helps examine how models use evidence on length-matched binary items.

As a complementary test across all 179 multiple-choice items, we compared full versus removed tool evidence for both Jev versions, averaging across original and reversed option orders. When full evidence was supplied, accuracy increased from 41.9% to 55.6% for Jev 1.13.0 and from 41.3% to 52.8% for Jev 1.14.0.

3. Reference answers and presentation. Two annotators independently reviewed the same 60 items blind to the reference answers. They agreed with the references on 58/60 and 56/60 items, respectively, and with one another on 54/60 items. In the revised manuscript, we have also added a worked Go/Git example and further clarified the task inputs and construction process.

Thank you again for your careful feedback. We hope that the additional binary control and manuscript revisions clarify our evaluation and its intended scope, and we would be grateful if you could take these results into consideration.

Reviewer_3uX3OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper presents the benchmark DoubleTakeBench that dedigned to evaluate fast models abillity to verify coding agents interpretations, rather than using heavy (slow and expensive) LLM reasoning.

The motivation is that current coding agents are working with the process of "Observe a tool result → Interpret what it means → Decide what to do next." which the authors argue that the interpretation step is a major source of errors (which might cause many tool calls trying to inspect a problem that never existed). They present the "Observation Judgment" as an operation, running by a faster model, reflecting on the agent's interpretation of each important tool observation before the agent acts on it.

Finally, the authors investigate confidence based routing, where uncertain judgments are delegated to a stronger LLM (with the heavy reasoning). This approach achieves 71.9% accuracy while reducing fallback LLM calls by 50%.

Critical strengths

S1. The motivation is compelling. It identifies an actionable failure mode inside coding-agent execution rather than treating the whole agent trajectory as a black box.

S2. The revision cycle examples are curated and originated from actual agent executions rather than synthetic examples.

S3. I appreciate the models variety tested to showcase the current benchmark phase.

Critical weaknesses

W1. It is not clear how frequent the misjudgments are in ordinary executions, because the dataset specifically selects episodes where they occurred.

W2. Absence of a live agent experiment ( offline could be good in testbed)

W3. The examples collected for the benchmark are only mistakes that the agent eventually recognizes and corrects. Since the data is the most important part in here, I wish to understand why did you avoid cases like "Agent misinterprets an observation, never notices and fails the task" or "Agent interprets an observation correctly immediately", which probably can be annotated by human, or frontier LLM observing the trajectories and enrich the data dramatically. Therefore, I'm concerned about the coverage and limitations of the revision cycle selection process.

W4. I agree that for production use using fast and cheap model as GLM flash for finding revision cycles is practical, but since its a benchmark that will serve others, I expect to have a stronger model to find them and to ablate this component while reporting this task False Negative.

W5. The experiments are isolating mainly the judge part, however in practice, discovering the relevant claim and identifying the correct evidence can be difficult, and therefore IMO it should be evaluated as full pipeline ( a complete monitoring system).

W6. Benchmarks are widely published nowadays, however, to make an impact on the communitiy, the benchmark must distinguish from others what its providing and why should one use me. Therefore, I must say that this motivation part is lacking, and I see what are you providing, but hard to tell why you and not others, maybe explaining the alternatives better and suggesting what have they missed in their benchmark design. For example, you have many LLM as a judge aspects in here, that are adapted to the coding domain, but the concepts are from a well researched domain, and I feel its missing in here. For example, I loved the motivation but felt that the benchmark is narrower than its motivation.

Questions for authors

Q1. Following W3, how many incorrect observation judgments never lead to an explicit self correction, and how might excluding them affect the benchmark's difficulty and representativeness?

Q2. According to the stats, for the true/false items, you have 188 negative statements based on original mistakes and 158 positive statements derived from corrected judgments - can you please explain what happened in the trajectories that you derived more than one negative statement.

Q3. What are the FP of GLM-5.3-Flash for finding revision cycles

Q4. Can you please share stats about human audited accuracy separately for positive, negative, and multiple-choice items? It will assist the average reader to understand the agreement between independent human annotators on a representative subset.

Q5. I appreciate the conclusion that reasoning-enabled models can do much better, however, can an SLM (Qwen 8B/32B for example) be trained to do so with the same efficiency while keeping the inference fast?

Q6. The fast judges are not perfect (far from it with many mistakes for both positive and negative aspects) -I wonder what would be the operational consequence of different FP and FN rates?

4 comments
AuthorsOpenReview ↗

Response to Reviewer 3uX3: Sampling, Human Audit, and Error Analysis

Dear Reviewer 3uX3,

Thank you for recognizing the motivation and the use of real execution traces. We clarify the benchmark's sampling and evaluation scope below, provide the requested human-audit breakdown, and quantify the judges' error trade-off.

W1, W3, Q1 — Sampling and coverage. Revision cycles identify concrete interpretation failures in real traces: an agent makes a judgment, then later revises it. The correction helps locate a candidate, and each reference answer is checked against evidence available at the original decision point. This gives a controlled diagnostic of local observation judgment. We will make this sampling frame explicit and extend the evaluation to independently sampled persistent errors and naturally correct first judgments, including estimating their frequency and effect on difficulty.

Q2 — Why 188 negatives and 158 positives? Directly usable corrections become positive items, while some originals are retained as negatives. This conversion and retention process gives the following counts:

Construction outcomeCount
Directly converted positives158
Negatives retained for balance59
Negatives restored after review18
Other negatives not converted: tradeoff / unsuitable / compound / unscreened69 / 26 / 15 / 1
Total negatives188

The binary majority baseline is 54.3%.

W3 — Construction cues. On the public binary release (346 items, 120 tasks), an evidence-free ten-feature classifier obtains 71.7% accuracy under five-fold task-grouped cross-validation, versus 54.3% for the majority baseline; two other split seeds give 69.4% and 68.5%. Character count alone gives 69.4–69.7% across the three seeds. We will report this wording signal alongside the benchmark results and investigate symmetric wording and naturally occurring positives as complementary controls.

W4, Q3 — Miner false positives and missed cycles. The 1,321-to-1,096 transition is selection for authoring under quotas. We will clarify the stages in Table 1. As a complementary coverage study, we will compare a stronger miner and independently review selected and unselected windows to estimate miner precision and recall.

Q4 — Human audit. Two annotators independently reviewed the same 60 items without seeing the reference answers. Agreement with the reference and between annotators was:

Item typenA vs. referenceB vs. referenceA/B agreement
Binary positive2020/2019/2019/20
Binary negative2018/2018/2016/20
Multiple choice2020/2019/2019/20
Total6058/6056/6054/60

We will include the detailed review tables in the project repository. This audit addresses reference validity; it is distinct from the wording-cue diagnostic above.

W2, W5 — Live agents and full pipeline. Supplying the same proposition and decision-time evidence isolates judgment quality across models. We will position the result as a controlled component evaluation and extend the evaluation to claim extraction, evidence retrieval, intervention, and live-agent success. The detour analysis quantifies tool calls associated with detected misjudgments.

Q6 — Consequences of FP/FN. On the archived binary snapshot:

JudgeErrors detectedErrors missedFalse alarms
simple-jev-27b104/18884/18832/158
TypeSafe109/18879/18846/158

TypeSafe catches five more errors but raises fourteen more false alarms. Misses leave errors unchallenged; false alarms interrupt correct progress. The trade-off depends on prevalence and intervention costs. The 71.9% cascade is an offline result with approximately 50% of items escalated to non-reasoning Claude Opus 4.8.

Q5, W6 — Smaller models and positioning. Training an 8B/32B judge is a useful follow-up; a fair evaluation needs task-disjoint data, calibration, and matched latency and context lengths. We will also add a comparison with ToolPRMBench and SWE-PRM: DoubleTakeBench isolates whether a factual interpretation follows from coding-tool evidence at decision time, complementing action-preference evaluation and trajectory-level intervention.

Thank you again for your thoughtful feedback.

Thank you,

my main concerns about benchmark validity and representativeness remain. Specifically, the new finding that an evidence free classifier reaches 71.7% accuracy which IMO raises further concerns about construction artifacts.

The sampling bias and lack of end2end validation also remain unresolved.

I therefore maintain my score.

AuthorsOpenReview ↗

Response to Reviewer 3uX3: Evidence-Based Judgment and Benchmark Coverage

Dear Reviewer 3uX3,

Thank you for your constructive follow-up regarding construction cues, benchmark coverage, and complete monitoring workflows. To address these points, we conducted paired evidence-control experiments on the released benchmark and have outlined our planned expansions to the evaluation framework.

1. Paired Evidence Controls

We evaluated Jev 1.13.0 on all 179 released multiple-choice items from 91 tasks. Each paired comparison uses the same question, background, state assumptions, and factual answer options; we vary only the tool-evidence field. Both conditions require a choice among the factual options (without INSUFFICIENT or DEFER) and are scored against the original reference answers. We test both original and reversed option orders and map reversed answers back to the original labels.

ConditionOriginal orderReversed order
Full tool evidence104/179 (58.1%)95/179 (53.1%)
Tool evidence removed72/179 (40.2%)78/179 (43.6%)

Across both option orders, full evidence increases mean item accuracy by 13.7 percentage points compared with the evidence-removed condition (5,000-replicate task-cluster bootstrap 95% interval: +3.2 to +23.7 points). For the original order, full evidence exceeds the content-masked control (75/179, 41.9%) by 16.2 points (95% interval: +4.9 to +26.9 points). In the masked condition, letters and digits are replaced by x/X and 0 while entry IDs, character counts, whitespace, and punctuation are preserved.

For binary questions, we tested Jev on all 346 released items using the proposition alone, with background, state assumptions, and tool evidence cleared. Jev reaches 206/346 (59.5%; AUROC 0.639), compared with a 54.3% majority-class baseline. The previously reported 71.7% is from a separate, supervised ten-feature classifier evaluated using task-grouped cross-validation. We will report these tests together to clarify the distinction between the Jev question-only test and the feature-based classifier.

2. Benchmark Coverage

DoubleTakeBench currently provides 525 decision-time judgment items derived from recorded coding-agent trajectories. To extend coverage, we have planned future experiments to sample additional decision points independently from full trajectories, including naturally correct first judgments and persistent errors. These will be verified against the evidence available at those specific points and reported separately by source stratum, then combined under the selected sampling protocol.

3. From Judgment to Monitoring

We plan to extend the evaluation to a monitoring workflow that integrates claim extraction, evidence retrieval, judgment, and intervention. The proposed comparative analysis will employ the same tasks and agent configuration with and without the monitor, reporting on task success, tool usage, and extraction and retrieval performance. This framework will connect the controlled judgment task to the broader monitoring workflow discussed in your review.

We will continue with additional experiments on independently sampled trajectory decisions and the complete monitoring workflow, including claim extraction, evidence retrieval, and judgment. As these results become available, we will update our response and revised manuscript with the new findings. We will also incorporate the paired evidence-control results into the paper and make the evaluation protocols and item-level predictions available alongside the benchmark. Thank you again for your constructive feedback and for the opportunity to strengthen our work.

AuthorsOpenReview ↗

Follow-up to Reviewer 3uX3: Evidence Controls and Trace-Based Retrieval

Dear Reviewer 3uX3,

We sincerely appreciate your thoughtful comments regarding evidence use, trajectory sampling, and the practical monitoring workflow. Your suggestions prompted us to examine how judges utilize supplied evidence and how retrieval from raw traces affects downstream decisions, which has helped us substantially strengthen our empirical analysis. Building on our initial response, we have completed two additional sets of experiments: we extended our paired evidence-control evaluation to a second Jev version, and we evaluated trace-based evidence retrieval followed by judgment on source trajectories.

1. Paired Evidence Controls Across Jev Versions

To better isolate the role of tool evidence, we evaluated Jev 1.13.0 and Jev 1.14.0 (both from the same model family) on the same 179 released multiple-choice items across 91 tasks. Each model answered under two conditions—with full tool evidence and with tool evidence removed—using both the original and reversed option orders. Both conditions require a factual choice; reversed answers are mapped back to the original option labels. Scores are averaged across the two option orders per item and evaluated against the original references.

ModelFull evidenceEvidence removedDifference
Jev 1.13.055.6%41.9%+13.7 pp
Jev 1.14.052.8%41.3%+11.5 pp

Providing full tool evidence improves accuracy by +13.7 percentage points for Jev 1.13.0 and +11.5 percentage points for Jev 1.14.0. Across 5,000 task-cluster bootstrap resamples, the exploratory 95% confidence intervals for these paired differences are +3.2 to +23.7 points for Jev 1.13.0 and +2.3 to +21.0 points for Jev 1.14.0. We will incorporate these results and the paired evaluation protocols into the revised paper and benchmark materials.

2. Trace-Based Retrieval and Judgment

Guided by your questions about connecting source trajectories to judgment, we also evaluated evidence retrieval followed by factual answer selection on 60 released multiple-choice items from 23 tasks with hash-verified source trajectories. Given the authored question and an endpoint determined by the reference evidence pointers, we retrieve three earlier trace steps using either question-based TF-IDF or a recency baseline. The trace prefix can include agent messages and reasoning. We then supply the three retrieved steps and the endpoint step to Jev for judgment.

Evidence suppliedJev 1.13.0Jev 1.14.0
TF-IDF top 3 earlier steps + endpoint37/60 (61.7%)34/60 (56.7%)
Most recent 3 earlier steps + endpoint34/60 (56.7%)33/60 (55.0%)
Original item evidence44/60 (73.3%)35/60 (58.3%)

Across these 60 items, TF-IDF top-3 retrieval achieves an item-averaged source-step recall of 42.8% of earlier referenced source steps, outperforming the recency baseline at 31.3% and yielding higher downstream judgment accuracy for both models. The original-evidence row reuses the corresponding full-evidence predictions; all three conditions use the same model-specific forced-choice and original-order evaluation.

These completed experiments directly connect trace retrieval to judgment using an authored question and a reference-located endpoint. In future work, we will evaluate independently sampled trajectory decisions and monitoring workflows, and we will update the revised paper as results become available. Thank you again for the time and care you devoted to helping us improve this work.

Reviewer_cH7gOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper presents a benchmarks which allows evaluating fast judgments in software developments (coding agents). DoubleTakeBench is a dataset of multiple decision-time judgment trajectories which allow evaluating the goodness of LLMs vs. fast system 1 models. The paper evaluates how the lightweight systems fare against LLMs and stratify the benefits across different confidence levels. This allows the authors to consider a hybrid approach where low confidence judgments from the fast system can invoke an LLM without losing on the benefits of using such fast system judgments for high confidence judgments.

Critical strengths
  • Release of a valuable benchmark that can help evaluate approaches for optimizing the system 1 and 2 tradeoffs for coding agents beyond what has been evaluated in this paper.
  • Sec. 6.4 and 7 which talk about the hybrid approach where we use System 1 for high confidence judgments and pivot to LLMs for low confidence one is quite valuable and worth exploring in practice.
Critical weaknesses

Sec 3.1 definitions of the task and items could have been explained better with examples especially when so many definitions were used

Questions for authors
  • Fix Fig 1
  • Use example to explain an item in Sec 3.1
  • Why was the drop from out of Screen Stage (1321) to In of Author stage (1096) in Table 1?
  • Is this a benchmark of the first of its kind? If the authors claim so, would be important to clarify that in the paper. If not, they need a comparison table with similar benchmarks to know why their is of more value.
2 comments
AuthorsOpenReview ↗

Response to Reviewer cH7g: Task Example, Construction, and Related Work

Dear Reviewer cH7g,

Thank you for recognizing the value of studying fast judgment and selective LLM use. We agree that the task and construction should be easier to follow. Below, we provide a worked item, explain the figure and funnel changes, and compare the task with closely related work.

Reply to W: Task Definition and Presentation

We will place a worked example before the formal definitions in Section 3.1.

An item asks whether a local interpretation is supported by the evidence available before the agent's next decision. The six-tuple records background, state assumptions, earlier commands and outputs, the question, answer options, and the reference answer. Only the first five components are supplied to the judge. Later events and the reference answer are withheld. A later correction helps locate a candidate; the earlier evidence must independently support its answer.

Reply to Q1: Consistency of Figure 1

We will use the same released proposition, options, and answer in the figure and Section 3.1.

The current figure asks whether ignore rules explain a file's omission, with answer Incorrect. The released item asks whether default Git behavior excludes untracked files, with answer Correct. These are different propositions. We will show the released version consistently, label the options A, Correct and B, Incorrect, and place the reference answer and explanation in a separate evaluator-only area.

Reply to Q2: A Worked Item for Section 3.1

The following shortened display maps a released example to the six components, making the input/output contract concrete.

ComponentExample content
BackgroundAdding //go:embed support to a Go interpreter
State assumptionsNo additional assumptions are supplied
EvidenceA command creates interp/embed.go, formats the touched files, and runs git diff --stat && git diff --check; exit status is 0, and the output lists five modified tracked files while omitting the new file
QuestionThe proposition quoted below
OptionsA, Correct; B, Incorrect
Reference answer, withheld from the modelA, Correct

The absence of the newly created interp/embed.go from this git diff --stat output is the normal result of Git's default diff excluding untracked files.

The full released packet contains the raw commands and outputs summarized above. Creating a file does not make it tracked, and default git diff excludes untracked files. The omission alone does not establish whether an ignore rule also matches it. No later correction is needed to answer this proposition.

Reply to Q3: Construction Funnel and Authoring Quotas

The reduction reflects per-task-quota selection for authoring, which we will label explicitly in Table 1.

Of 1,321 screened cycles, 1,096 are selected under the quotas. The difference of 225 is therefore a selection count, not a count of invalid cycles. Authoring produces 551 items, including 14 pilot items; preflight leaves 549, and verification and adjudication leave 525. We will distinguish cycle counts from item counts and identify pilot inclusion in the table caption.

Reply to Q4: Positioning Against Existing Benchmarks

We do not rely on an absolute first-benchmark claim; the contribution is the specific observation-judgment task.

WorkEvaluated objectEvaluation question
SWE-benchRepository issue and codebaseCan the agent resolve the issue?
ToolPRMBenchInteraction history and candidate tool actionsWhich action is preferable at this step?
SWE-PRM, an intervention methodCoding-agent trajectory during executionCan feedback detect and correct trajectory inefficiencies?
AgentRewardBenchWeb-agent trajectoryCan a judge assess success and trajectory properties?
ProcessBenchMathematical solutionWhere is the first reasoning error?
DoubleTakeBenchLocal proposition and earlier coding-tool evidenceIs this interpretation supported at the decision point?

ToolPRMBench and SWE-PRM are particularly relevant comparisons. Step-level evaluation and online feedback already exist. Our narrower target is whether a factual interpretation follows from an observed command and output, before choosing the next action. For example, interpreting an omitted file is distinct from ranking candidate next commands. Holding the proposition and evidence fixed supports controlled comparisons of fast judges and LLMs, including option-order sensitivity and selective routing. We will move this distinction into the main-text comparison and state the revision-cycle sampling boundary explicitly.


Thank you again for your time and the opportunity to address your concerns.

Best regards, The Authors

AuthorsOpenReview ↗

Follow-up to Reviewer cH7g: Clearer Task Presentation and Manuscript Updates

Dear Reviewer cH7g,

We would like to thank you again for your detailed and constructive suggestions regarding our task presentation, data-construction accounting, and positioning within the broader literature. Your feedback highlighted several areas where our exposition could be much clearer for the reader, and we have prepared three concrete updates for the revised manuscript based directly on your recommendations:

  1. Worked example and Figure 1. To ground the task formulation earlier, as you suggested, we now introduce the worked Go/Git example prior to the formal definitions in Section 3.1. We have also fully aligned Figure 1, the question text, answer options, and the reference answer with the released benchmark item, explicitly distinguishing decision-time inputs from the evaluator-only reference answer.
  2. Construction accounting. In response to your point about clarity in our filtering pipeline, we have updated the construction table to explicitly label the transition from 1,321 screened cycles to 1,096 cycles selected for authoring as per-task-quota selection, and we now clearly distinguish cycle counts from final item counts.
  3. Related work comparison. Building on your advice to better contextualize our contribution, we have prepared a structured comparison detailing the evaluation objects and question formulations across related benchmarks and methods, including ToolPRMBench, SWE-PRM, AgentRewardBench, and ProcessBench.

We will incorporate these prepared presentation updates into the revised manuscript and release the evaluation protocols and item-level results alongside the benchmark. We sincerely appreciate your careful reading of our paper and your guidance in making the manuscript much clearer and more accessible.

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Rebuttal Summary to the Area Chair

Dear Area Chair,

Thank you for managing the review process. We appreciate the reviewers' careful feedback, which helped us clarify the benchmark and add targeted analyses. We have submitted a revised manuscript and summarize below our core contributions and the primary updates from the discussion period.

1. Contributions recognized by the reviewers. DoubleTakeBench studies a concrete decision within coding-agent execution: whether an interpretation of a tool observation is supported by the evidence available at that point. Reviewer 3uX3 found this to be an actionable failure mode and valued our use of real execution traces; Reviewer cH7g highlighted the benchmark's utility for studying fast judgments and the selective deployment of stronger models. By holding the interpretation and evidence fixed, the benchmark enables direct comparison of judges on this specific decision.

2. Targeted validation added during the discussion.

  • Human reference check (Reviewers 3uX3 and yU4a). Two annotators independently reviewed the same 60 items (20 positive, 20 negative, and 20 multiple-choice) blinded to the reference answers. They agreed with the references on 58/60 and 56/60 items, and with each other on 54/60 items. Our individual responses provide the full breakdown by item type.
  • Evidence controls (Reviewers 3uX3 and yU4a). Across all 179 multiple-choice items from 91 tasks, we compared evaluation with full tool evidence against evaluation with evidence removed, averaging across original and reversed option orders. With full evidence, accuracy increased from 41.9% to 55.6% for Jev 1.13.0, and from 41.3% to 52.8% for Jev 1.14.0. The revised manuscript reports these paired controls.
  • Binary construction controls (Reviewer yU4a). We conducted question-only tests and a supervised text-feature diagnostic, and additionally analyzed 228 binary items selected retrospectively as 114 length-matched positive/negative pairs. For Jev 1.13.0 on this subset, accuracy was 62.7% with full input compared to 57.0% with tool evidence removed; the exploratory task-cluster bootstrap 95% confidence interval for the difference was −3.0 to +14.6 percentage points. We report the matching procedure, text-only controls, and full results in our follow-up reply.
  • Trace retrieval and judgment (Reviewer 3uX3). On 60 released multiple-choice items from 23 tasks, we evaluated step retrieval followed by judgment using the authored question and a reference-located endpoint. Retrieving three earlier steps via TF-IDF yielded 61.7% and 56.7% accuracy for Jev 1.13.0 and 1.14.0, respectively, compared with 56.7% and 55.0% using a recency baseline. The protocol and results are now included in the appendix of the revised manuscript.

3. Clearer presentation and positioning. In response to Reviewer cH7g, we added a worked Go/Git example, aligned Figure 1 with the corresponding released item, and clarified that the reduction from 1,321 screened cycles to 1,096 cycles selected for authoring resulted from per-task quotas. We also added comparisons with ToolPRMBench and SWE-PRM to better distinguish observation judgment from evaluating candidate actions or intervening in trajectories. In response to the sampling questions from Reviewers 3uX3 and yU4a, we clarified the benchmark's revision-cycle construction and task definition. In future work, we plan to extend the evaluation to independently sampled trajectory decisions, including naturally correct judgments and persistent errors.

We sincerely thank the reviewers for their constructive feedback and the Area Chair for considering our responses, additional evidence, and revised manuscript in the overall assessment.

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

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