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Desk rejected at ICLR 2027

Beyond Execution: Auditing Experimental Fidelity in LLM-Driven Scientific Research

Desk rejected at ICLR 2027, so left out of the paper lists and the map.

Abstract

LLM agents are increasingly used to reproduce and extend scientific experiments, and their output is often judged by whether the generated code runs and reports plausible metrics. We argue that this criterion is insufficient and study methodological hallucinations: silent deviations from a reference experimental protocol that leave execution intact but undermine the scientific conclusion. Examples include reducing datasets or training budgets without reporting it, replacing a failed learning or generative component with a lookup or oracle function, and drawing conclusions at a scale where the method's claimed advantage cannot appear. From a case study of 30 long-horizon reproductions of machine learning papers under a single consumer-GPU budget, we derive a five-class taxonomy of such failures. 17 of the 30 runs (56.7%) exhibit at least one, even though every run was produced by an agent that had the reference protocol in its prompt. To make such deviations easier to surface, we describe ABE-Ralph, a lightweight auditing protocol that encodes a paper's claims, required components, baselines, and metrics as a YAML contract, guides implementation through an 8-step workflow, and applies three inexpensive post-hoc checks: result coverage, LLM-based semantic review, and module presence. In a single-run comparison with four agent baselines, ABE-Ralph obtains the highest composite score (58.8, versus 51.0 for the strongest baseline) on a 21-task set whose per-system coverage differed (10–18 of 21 tasks). Because the systems also differ in backbone model and iteration budget, however, we cannot attribute this gap to auditing alone. Our findings suggest that evaluations of AI scientists should check whether an experiment faithfully tests the intended claim, not only whether it runs.

Primary area:
datasets and benchmarks
Keywords:
LLM Agents, Reproducibility, Hallucination Detection

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_XqfXOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

The author found that in the field of AI for Research, even when experimental requirements are repeatedly included in the prompt, agents still quietly alter the experimental conditions. The author refers to this phenomenon as methodological hallucination, categorizes the different types of distortion, and proposes a method called ABE-Ralph. This approach requires the model to clearly write out the experiment first before checking the execution outputs, and small-scale experiments are conducted to demonstrate the method's effectiveness to a certain degree.

Critical strengths

The author's observation is meaningful.

Critical weaknesses
  1. The method claimed by the author does not actually work in practice. One of the three checks designed by the authors was never actually executed, specifically the L3 critical modules. They didn't fill in the required critical modules in any of the thirty experiment runs, so they all defaulted to passing. In other words, the authors completely failed to implement what they claimed to do in their own method. It looks like they didn't even check their own work before submitting it so irresponsibly.
  2. The experimental setup used by the authors may invalidate their claim, as all experiments were run on a single 4070 GPU. It is possible that the limitations observed in the models were entirely hardware-driven. The authors had the models perform various tasks involving language models like BERT, as well as other generative models such as DDPM and DDIM. This raises concerns about whether these architectures can theoretically even run properly on an RTX 4070. The authors claim to have identified problems in the agent, but in reality, this failure to complete the tasks could simply be due to hardware constraints.
  3. The writing in this paper is very poor. For instance, Figure 1 is extremely small, and the text on it is completely illegible. Furthermore, the various bar charts later on are inconsistent in style and have different background colors, as if they were screenshotted from somewhere else. There are also some obvious typos. For instance, the percentage sign is written twice everywhere. The author didn't even bother to read through their own paper.
  4. The authors didn't run experiments on recognized or complete datasets. Therefore, the paper lacks a complete evaluation and fails to support any of the claims the authors are making.
Questions for authors

NA

4 comments
AuthorsOpenReview ↗

Response to Reviewer XqXf (1/3)

Thank you for auditing the audit.

P1 — none of the three checks was ever executed

L1 and L2 ran; L3 did not. L1 wrote a verdict in 47 workspaces of the archive, 23 of the 30 benchmark runs among them; across the 47 the split is MET_ALL 8, MET_PARTIALLY 29, FAILED 9, UNKNOWN 1. L2 wrote 11 review logs, 6 with a parseable DECISION. L3 was vacuous because no contract declares critical_modules — a field that is optional in the schema and was omitted by the generator in all 30.

Table 5 — what the archive carries, per benchmark run

ArtifactPresentAbsentConsequence
Final run report25/305: bm_018, bm_022, bm_024, bm_025, bm_030nothing for L2 to read; they are outside Table 2
Stored L1 verdict23/307: bm_018, bm_022, bm_024, bm_025, bm_028, bm_029, bm_030L1 cannot be re-checked on those
results/metrics.json21/309: bm_019–bm_021, bm_022–bm_025, bm_027, bm_030L1's quantitative stage returns METRICS_MISSING and is skipped
Every contract metric has a stored field18/21 of the runs with a filebm_003 2/3, bm_007 2/3, bm_016 1/2partial coverage of what the contract asked for
Stored value appears in the run's own report50/55 values (91%)5: two in bm_008, one in bm_026, two in bm_018, which has no reportpresence, not agreement — bm_006 passes this test while its headline number contradicts the file

The row is loose by construction — a match on any spelling from one to four decimal places counts — and we flag it as the one number here that flatters us.

With critical_modules populated from the papers and run on the stored code, L3 does no better than vacuous, and the reason is scope rather than absence of components.

Table 6 — L3 with critical_modules populated, 20 runs and 62 components

ScopeNames matchedRuns passing
as implemented: <workspace>/main.py only3/620/20
whole workspace, exact identifiers7/62—
whole workspace, spelling-normalised53/62—

The component code is there; the check looks in the wrong place. Nine names appear in no file at all — DualEncoder; BERT's TransformerEncoder, MaskedLM and NextSentencePrediction; GapSentenceGeneration; DilatedAttention; ContrastiveLoss; and U-Net's ContractingPath and ExpandingPath — so name normalisation is needed as well as scope. A revision would either fix both or remove L3 from the protocol.

AuthorsOpenReview ↗

Response to Reviewer XqXf (2/3)

P2 — "everything ran on one 4070", and what was actually run

Half right, and the wrong half is ours. Every run executed on one RTX 3080 with 12 GB. The hardware check at the head of the run log prints NVIDIA GeForce RTX 3080, total_memory: 12.0 GB, compute capability 8.6, 20 CPU cores (bm_006_lora_lora/run_all.log:24-31; the same block appears in ten workspaces spanning four batches), and in bm_012 the agent's own experiment_state.json records NVIDIA GeForce RTX 3080 (12 GB VRAM) — exceeds the plan's RTX 4070 Laptop (8 GB). The RTX 4070 Laptop / 8 GB line in all 30 contracts is the budget the agent was given, not the machine it ran on; §5.1 reproduced it as a description of the host.

Erratum: the sentence should read "a single RTX 3080 (12 GB VRAM), with per-run time budgets drawn from the reference contracts (median 27 h, range 10–58 h)" — the recomputed median is 27 h, not 26. The report lines naming the 3080 were right, and we had read them as an error. Neither verify_reproduction.py nor alignment_verifier.py inspects hardware, which is how an unverified configuration value reached the settings paragraph — the failure the taxonomy exists to catch, in our own paper.

The argument is unaffected. On one consumer card, ViT from-scratch pre-training, ImageNet-scale training and MuJoCo control stay out of reach; the ViT run stays M2+M3+M5 (trained from scratch, scale-dependent conclusion, neither declared). The card was binding: the PEGASUS report lists Constrained batch size as the price of running on RTX 3080 12 GB (bm_008).

The clock, by contrast, was never close. Nine of the 30 reports state how long the run took, and every one finished well inside its contract budget.

Table 7 — contract compute budget against the runtime the run itself reports

Runmax_gpu_hoursStated runtimeShare used
bm_008 PEGASUS3667 min3.1%
bm_014 CLIP1227 min3.8%
bm_019 YOLO180.75 h4.2%
bm_020 PatchCore2460 min4.2%
bm_006 LoRA2477 min5.3%
bm_009 LED486.5 h13.5%
bm_005 RoBERTa244.5 h18.8%
bm_013 ViT308.5 h28.3%
bm_015 SimCLR3612 h33.3%

The median run used 5% of its budget and the largest share 33%: M5 records runs that stopped incomplete rather than runs that ran out of time. The other 21 reports state no runtime, so this is a lower bound on coverage, not a summary of the corpus.

Table 8 — what each labelled run executed, as its own report states it

RunLabelPaper's settingExecutedWhere its own report says so
bm_026 PPOM2+M5nine MuJoCo continuous-control tasksCartPole-v1 (discrete), 3 seeds, 100K timestepsSummary; the conclusion speaks of "continuous control tasks" without the substitution
bm_004 BERTM2+M5full GLUE suiteSST-2, MRPC, QQP; ≥3 epochsheader; §1
bm_015 SimCLRM1+M2ResNet-50, batch 4096, 800 epochsResNet-18, batch 256, 400 epochs on CIFAR-10header table; §5
bm_003 ColBERTM2+M5~200K training steps500 steps, 500 queries, 82K passagesheader; gap attributed to "reduced training scope"
bm_008 PEGASUSM2+M3+M5287K CNN/DailyMail examples3,000 samples, 2 epochs (1.2%)§3 table; §8 says absolute ROUGE not reproduced
bm_013 ViTM2+M3+M5ViT-B/16 pretrained on JFT-300M, fine-tunedImageNet-pretrained at 93.29%, from scratch at 26.02%§2 results table; §7
bm_017 U-NetM3+M5full ISBI 2012 (30 images)30 epochs on 24 training images (6 held out)§4; §6 qualifies the claims by scale
bm_028 GraphSAGEM2+M4+M515 epochs, hidden 256, batch 5125 epochs, hidden 64§5; skipped conditions listed

These are all the runs carrying M2 or M3 except bm_018, which produced no report. The scale is recoverable from the report in all eight cases; what varies is where it sits. PEGASUS and GraphSAGE put it in the conclusions; PPO names the environment only in the summary line and then generalises to "continuous control tasks".

AuthorsOpenReview ↗

Response to Reviewer XqfX (3/3)

P3 — Figure 1 and formatting

Figure 1 is a 1487×578 raster, set at 0.62\textwidth in the submission, which puts its labels near 4–5 pt. In the rebuilt PDF it runs at full width and they are legible; a revision would re-export it at ≥8 pt. We rebuilt the PDF and fixed the typos.

P4 — datasets used at reduced scale

The canonical datasets are used at reduced scale: GLUE, NaturalQuestions, TriviaQA, MSMARCO, CIFAR-10/100, ImageNet subsets, ISBI, PASCAL VOC, Cora/Citeseer, MuJoCo. The reductions are the object of study, not an accident, and Table 8 gives that account for every run carrying M2 or M3.

Ethics flag

We take the flag seriously. It rests on the concern that results were reported that the authors did not produce. Each factual claim in the review is answered against a file in the archive that Table 5 inventories, and Appendix F reports the runs where our own pipeline failed: PEGASUS −32% against BERT, and PPO claiming continuous-control success while none of the nine MuJoCo runs completed. Those are in the labelled corpus with the same labels we apply to the agents. We will answer any specific question about any artifact.

Thank you for the response. The rebuttal confirms that L3 was never effectively executed and that the hardware setup was misreported. These issues undermine the reliability of the audit itself. I will keep my score.

Reviewer_2gdVOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The paper studies methodological hallucinations: undeclared departures from a reference protocol that make an experiment scientifically misleading despite apparently successful execution. Its five categories cover method integrity collapse, silent protocol degradation, scale-driven conclusion inversion, quantitative key mismatch, and incomplete execution.

A case study of 30 ABE-Ralph reproduction runs finds at least one labeled failure in 17 runs, or 56.7%; an alternative treatment of disclosure reduces this to 12 runs, or 40.0%. ABE-Ralph combines LLM-generated YAML reference contracts, an eight-step workflow, and three post-hoc checks. The main contribution is an empirical taxonomy and set of cases. The auditing implementation is lightweight and not yet validated as an effective detector or preventive mechanism.

Critical strengths
  • The paper identifies a practical problem of methodological hallucination, useful for people relying on research agents. The study shows that agents can silently reduce experiments or fail to disclose incomplete work under limited computing resources, even when repeatedly given the intended protocol.
  • The five failure categories and concrete cases give readers a useful way to describe what went wrong. The rules also distinguish an unfaithful experiment from a faithful experiment that simply does not reproduce the expected result.
Critical weaknesses
  • The paper does not establish how accurately the auditor detects failures. No detection precision or recall is reported, the module check passes automatically in all annotated runs because no required modules are listed, and the remaining verdict depends on a judge that reads only the final report.
  • The system scores are difficult to compare because they average different task subsets and use different resource budgets. Only ABE-Ralph runs were labeled for scientific fidelity.
Questions for authors
  • Did all systems use the same underlying model, and which tasks did they have in common? The main text and appendix give different descriptions. If available, what are the scores for ABE-Ralph and Claude Code CLI on the same tasks?
  • Did you check the failure labels against the original papers or against the generated contracts? Do any labels change when errors in the contracts are corrected?
1 comment
AuthorsOpenReview ↗

Resopnse to Reviewer 2gdV

Thank you for the four questions; they go to what the RQ1 table can and cannot support.

Q1 — same model, common tasks

Same model (deepseek-v4-flash) for all five systems. Coverage ran from 10 to 18 of the 21 tasks (ABE 10; ARC, Claw-AI-Lab and Claude Code CLI 18; Raw LLM 15), and the scores are ABE 58.8, Claude Code CLI 51.0, Claw-AI-Lab 39.9, ARC 33.0, Raw LLM 30.8 — single runs, no variance estimates.

Q2 — labels versus contracts, and contract errors

Against the original papers for M1, M2, M3, M5; against the contract's metric keys for M4. The DPR error changes no label. The remaining contract corrections will be checked class by class and any change reported.

Q3 — fairness of the RQ1 comparison

Not fair, and we say so in the paper: coverage, iteration budget and token usage were not matched (the model is settled under Q1). The ranking is descriptive only, and a revision reports the intersection-restricted RQ1 with the per-task matrix.

Q4 — robustness of 56.7% and 40.0%

The two figures are the two readings of the same label file, and the difference is a single judgement.

Table 4 — label distribution behind the headline numbers

M1M2M3M4M5CleanAny label
Runs (N = 30)3832151317
Share10.0%26.7%10.0%6.7%50.0%43.3%56.7% (40.0% strict)

Labels number 31 in total, so failures co-occur. Five runs carry M5 alone: counting their incomplete output as declared gives 12/30 = 40.0%. The 12 runs carrying M1–M4 do not depend on that judgement. A revision would report both readings whenever it reports either.

Reviewer_icDQOpenReview ↗
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1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

This paper studies methodological hallucinations in LLM-driven scientific reproduction: undisclosed deviations from a reference protocol that make apparently successful experiments scientifically misleading. It proposes a five-class taxonomy and analyzes 30 reproduction runs under constrained compute, finding such failures in 17 runs, or 12 under a more conservative disclosure criterion. The authors also introduce ABE-Ralph, which combines structured reference contracts, an eight-step workflow, and three post-hoc auditing checks. Evaluation includes the annotated case study, comparisons with four baselines, and instruction ablations. The findings motivate evaluating experimental fidelity beyond successful execution, although the system comparisons are confounded and the auditor’s detection accuracy remains unvalidated.

Critical strengths
  1. Useful taxonomy. Clearly distinguishes methodological deviations from genuine reproduction failures.

  2. Informative case study. Documents fidelity failures despite explicit protocol guidance across 30 resource-constrained runs.

Critical weaknesses
  1. Unvalidated auditor effectiveness. The verdict relies on an LLM judging the final report without inspecting code or logs. No detection-accuracy evaluation demonstrates that it catches hidden protocol violations.

  2. Confounded system comparison. Systems are evaluated on different task subsets with unmatched models and budgets, making the reported score advantage difficult to attribute to the proposed workflow.

  3. Unverified reference contracts. The generated contracts lack systematic human verification and contain an acknowledged error. Their impact on failure labels and audit decisions remains unclear.

Questions for authors
  1. How well do the audit decisions agree with the verified labels on the 30 annotated runs?

  2. Were the labels verified against the original papers, and how were contract errors handled?

  3. How does ABE-Ralph compare with the baselines when evaluated on the same task subset?

2 comments
AuthorsOpenReview ↗

Resopnse to Reviewer 1cDQ (1/2)

Thank you for the close read of our protocol; the detection-accuracy question is what sent us back to the archive.

W1 / Q1 — a judge that reads only the report, and how closely it agrees with the labels

W1 and Q1 are one question: W1 asks for a detection-accuracy evaluation, Q1 asks what it shows. We answer both here.

Correct about the shipped L2: its declared input was the report and the contract. The archived logs qualify it on two counts: in the bm_001 call the judge also opened metrics.json and experiment_output.log, and in that same call it read a sibling batch directory — a contamination bug we fixed on 2026-11-12. We also re-ran the same prompt with the artifacts inside it, on ten runs: the eight the shipped L2 got wrong and two it got right.

Table 1 — the same judge, with the artifacts in the prompt (10 runs: the 3 false positives, the 5 misses and the 2 correct flags of the shipped judge)

Judge, on these 10 runsTPFPFNTNPrecisionRecall
L2 as shipped23500.400.29
L2 with metrics.json and the log tail in the prompt73000.701.00

With the stored metrics and the tail of the run log pasted in, all five misses are caught and both correct flags hold; the three clean runs stay flagged. The sample is not random, so these counts are not comparable to Table 2 — what they show is the direction.

One of those three clean runs is not clean. In bm_006 the report's headline — full fine-tuning at 0.509 accuracy, LoRA ahead by 0.42 — contradicts the archived metric file, which records 0.9255 for the same condition, and the file is timestamped three hours after the report. We do not settle here which number is right. The point is that the archive disagrees with itself and the label was assigned from the report.

Table 2 — the auditor against the labels, by stage and by judge

CheckJudgeFlagged whenTPFPFNTNPrecisionRecallκRuns
L2: report + contractclaude CLIany non-MET_ALL73530.700.580.0818
L2: report + contractclaude CLIonly FAILED101161.000.080.0618
L2: report + contractqwen-maxany non-MET_ALL65620.550.50−0.2119
L1: metrics.jsondeterministicany non-MET_ALL116330.650.790.1323
L1: metrics.jsondeterministiconly FAILED50991.000.360.3023

Three clean runs are flagged (lora, longformer, clip) and five labelled runs pass (bert, simclr, unet, yolo, patchcore); those eight are the runs Table 1 works on. Two of the 20 runs are outside the L2 matrix: one produced no report, one gave no parseable verdict.

The 0.08 is not a property of the judge. The same prompt, sent verbatim to a second model family, gives −0.21 over 19 runs and agrees with the first judge on 15 of them: what the report alone supports is at chance whichever model reads it.

The quantitative stage behaves differently. When L1 says FAILED, all five of those runs carry a label; its κ is 0.30 at the threshold where L2 scores 0.06. Its recall is 0.36 because a metric check cannot see the majority class — an M2 run degrades silently and still leaves plausible numbers. The auditor's output space is three verdicts, so per-class precision and recall over M1–M5 are not computable from it without changing that format.

The fix is structural: a revision would make the artifacts the first stage of the verdict and the report the second.

W2 / Q3 — models, budgets, and scores on a common task set

One question from two sides. The model is not a confound; the task set is.

All five systems' API calls resolved to deepseek-v4-flash in this environment (AI Use Statement). Iteration, token and wall-clock budgets did differ, and coverage ran from 10 to 18 of the 21 tasks, so the RQ1 gap cannot be attributed to the contract workflow on that basis; Appendix I says so. What we do not have is the per-task matrix Q3 asks for: the archive holds per-run scores for ABE but no matched per-task scores for the four baselines, and the ABE figure in RQ1 comes from a different task subset. A revision would reconstruct it and report intersection-restricted means with per-task values. Until then the ranking should be read as descriptive only, and the abstract should not imply it.

AuthorsOpenReview ↗

Resopnse to Reviewer 1cDQ (2/2)

W3 / Q2 — contract provenance, and whether the labels were verified

W3 asks whether contract errors reach the labels; Q2 asks how the labels were verified and how contract errors were handled.

Labels were assigned from each run's report against the original paper for M1, M2, M3 and M5. Only M4 is defined on the contract's metric keys, and it covers 2 of 30 runs. The one documented contract error — the DPR contract presents in-batch negatives as more sample-efficient than hard negatives, where the paper reports that adding BM25 hard negatives helps — changes no label: DPR is Clean, because the run reproduces what the paper reports. Had the labels been read off the contracts, that run would have been mislabelled. The contracts are GPT-4.1-generated from the source papers and were never human-verified; we treat them as reference contracts rather than ground truth, and say so in §3.2 and Appendix I.

Verification happened and left a trace in the released file: 15 of the 30 rows carry a verification note, and three were relabelled (BERT M1→M2; SimCLR M3→M2 with a duplicate M5 removed; Improved DDPM M1→genuine failure). The paper is explicit that inter-annotator agreement was not measured (§5.1). We measured it. A second coder — a different model, given only the five decision rules, the three boundary rules, the contract and the report, i.e. the same inputs the authors had — re-labelled a stratified subsample of 12.

Table 3 — second coder on a stratified 12-run subset

ClassBothSecond coder onlyAuthors onlyκ
M10010.00
M25600.12
M30020.00
M40010.00
M58200.57

Exact label-set agreement 4/12. On the coarser question — is the run affected at all — 9/12, κ = 0.31, and the disagreement is one-sided: the coder flags 11 runs against our 8. It is better at saying that a run is affected than at naming the rule that was broken, and it errs towards over-flagging, which is what a coder reading the report alone does. M5 is recovered best; M1, M3 and M4 are never assigned, which is what we expect, because those three need the original paper's scale regime or the contract's metric keys rather than a single report. It also applies M2 to 11 of the 12 runs, which is why that row's κ is low while its raw overlap is not.

The M2 disagreements have one shape, and it is ours to fix. In bm_010 the report writes "Reduced-scale (500 samples/condition, 20 epochs)" and the coder still labels M2, on the grounds that the reduction's effect is not stated. Boundary rule (ii) says a declared deviation is not M2. We meant that the declaration has to give the value (500 samples, 20 epochs); the coder required it to give the consequence as well. A revision would write the rule as a test — the executed value must appear in the same section as the claim it limits — which is the column Table 8 fills.

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

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