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Paper summary
The paper identifies a gap in current factuality evaluation for long-form answers. The dominant paradigm, established by FActScore and followed by FACTS Grounding and subsequent work, decomposes an answer into atomic claims and verifies each claim in isolation. This "independence assumption" overlooks the reasoning structure internal to the answer: later interpretations typically take earlier observations as premises, forming a dependency graph over the answer. The paper's Figure 1 illustrates the consequence: when an observation is contradicted by the source, interpretations built on it are still labeled "supported" by claim-level verification, because in isolation each interpretation can indeed be found in the source.
The authors name this failure INVALIDSUPPORT and build a benchmark, MMSciFact, to make it measurable: 45 papers, 257 question–answer pairs, and 2,737 answer sentences, spanning three evidence scopes (single-page, cross-page, full-paper). Each instance pairs a paper and a question with an MLLM-generated long-form answer whose errors occur naturally and are neither injected nor corrected. Expert annotators label sentence roles, cross-sentence dependencies (forming a DAG), and grounding labels (SUPPORTED / CONTRADICTED / NEI / INVALIDSUPPORT). In total, 148 sentences (5.4% of all sentences) are labeled INVALIDSUPPORT, affecting 23% of answers. Evaluation is conducted under three settings: Independent (dependencies ignored), Holistic (the judge must infer dependencies itself), and Oracle-graph (annotated roles and dependency graph are provided).
Key findings: across 12 MLLM judges, current models remain weak scientific fact-checkers, strongly over-predicting SUPPORTED, struggling most with NEI, and showing limited evidence-localization ability. INVALIDSUPPORT is hard to detect when judges must infer dependencies themselves; providing the annotated dependency graph improves its detection substantially (significant for 9 of 12 judges), yet absolute scores remain low even then.
Critical strengths
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The problem is well identified and targets a genuine blind spot in the prevailing evaluation paradigm. The observation that claim-level verification misses conclusions built on false premises is conceptually clear, is illustrated convincingly by Figure 1 and the constructed examples in the three judge prompts, and is indeed not covered by existing scientific fact-checking benchmarks (Table 1).
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INVALIDSUPPORT is a label of real value, and it is formally defined. The paper gives an explicit decision rule (an interpretation that would be SUPPORTED on its own, at least one of whose direct or transitive premises is CONTRADICTED or NEI) and separates "whether the conclusion itself holds" from "whether the premises supporting it hold" — a distinction of practical importance in scientific settings.
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The three verification settings constitute a sound diagnostic design. The progression Independent / Holistic / Oracle-graph separates three distinct situations — not modeling dependencies, having to recover them, and having them given but still needing to use them correctly — which is the most methodologically valuable aspect of the paper.
Critical weaknesses
W1 INVALIDSUPPORT is the paper's central contribution, yet its two causes are reported jointly and the alternative explanation — that the premises themselves are misjudged — is not ruled out
INVALIDSUPPORT is the only new label relative to prior benchmarks (Table 1) and the anchor of every conclusion in the paper. Yet it is reported as a single quantity:
- Table 3 gives one INV column, with no breakdown by cause.
- Appendix F defines a complete error-code taxonomy (C1–C3 for factual misread, visual misinterpretation, and relational error; N1–N3 for fabricated evidence, unsupported inference, and overclaiming conclusion), together with two dedicated propagation codes: C4 (false-premise conclusion), for a conclusion built on premises contradicted by the source, and N4 (unverifiable-premise conclusion), for one built on unverifiable premises. However, neither the main text nor the appendix reports the distribution of these codes — I could not find sentence counts for C1–C3, N1–N3, C4, or N4 anywhere in the paper.
C4 and N4 are tasks of a different nature:
- C4 requires the judge to locate an explicit contradiction in the document; there is a locatable erroneous element to point at.
- N4 requires the judge to determine that the document never says this at all, which is detection of absence with no location to point to.
Table 3 already shows that among the three labels shared across settings, NEI has the lowest F1 under every setting. The central question is therefore: does the difficulty of detecting INVALIDSUPPORT come mainly from premises that are falsified (failure of dependency reasoning), or mainly from premises that cannot be verified (NEI-detection failure amplified along the dependency chain)? If the latter predominates, the paper's central finding is closer to "models cannot recognize missing evidence," with INVALIDSUPPORT merely amplifying a known weakness; only if the former predominates is it the new bottleneck, independent of grounding, that the paper claims. The current reporting cannot distinguish these two explanations, and they carry very different implications for the paper's conclusions.
A related argumentative gap appears in Section 5. The paper claims that because INVALIDSUPPORT remains low even when the annotated dependency graph is provided, recovering and reasoning over sentence dependencies constitutes a bottleneck distinct from evidence grounding. That inference skips an intermediate step: to label a sentence INVALIDSUPPORT correctly, the premise it depends on must first be judged CONTRADICTED or NEI. Yet CON F1 is only 0.1–0.6 and NEI only 0–0.4, so when premises themselves are misjudged, the judge never reaches INVALIDSUPPORT at all. "Low INV under Oracle-graph" therefore admits at least two explanations: (a) the judge cannot use the given dependency structure, or (b) the judge cannot even ground the premise sentences correctly. The "distinct bottleneck" claim requires (b) to be ruled out first, and no such conditional analysis appears in Appendix E (E.1–E.8).
W2 Domain coverage of the sources, and the validity confound introduced by pretraining memorization
Domain coverage. The introduction states that the sources are "drawn primarily from computer science," so the wording does not itself claim cross-domain generality. Per Appendix Figure 4, however, the topic distribution of QA pairs is: multimodal / vision-language 28%, biology & life sciences 13%, factuality, grounding & RAG 12%, summarization & text clustering 10%, LLM evaluation & generalization 8%, ML methods & architecture 7%, biomedical & clinical NLP 5%, with all remaining topics below 5%. Roughly three quarters of the instances therefore come from within NLP/ML, while physics, chemistry, materials science, earth sciences, and the social sciences are essentially absent. In addition, the 45 source papers were nominated by 12 authors with NLP/ML backgrounds (each paper contributing only about 6 QA pairs), and the venues cluster in ICLR / *ACL / NeurIPS (about 50%).
This raises a direct question: are the failure modes characterized here domain-general? The observation–interpretation distinction and dependency structure are common across the sciences, but the present data provide no evidence for cross-domain applicability. Appendix A already concedes "limiting source diversity and potentially introducing selection bias," yet the framing in the abstract and main text ("scientific fact-checking") is broader than the data support. I would suggest the authors either narrow the corresponding claims or add a discussion of domain coverage.
Pretraining memorization. The paper's treatment of leakage risk is confined to one sentence in Appendix A: public source papers may appear in pretraining data, but the questions, answers, dependency structures, and labels are newly created, which reduces the risk of instance-level contamination.
I do not think this argument covers the main risk in this setting. The task here is to judge whether a sentence is grounded in a given document, not whether it holds in the open world. The primary risk is therefore not that the model has seen this QA pair, but that the model has seen the source paper itself — if so, it can answer from memory rather than actually reading the few pages of evidence it is given. What is then measured is closer to recall than to grounding ability, which is precisely what the paper sets out to measure. The confound is further amplified by the paper's design: the single-page / cross-page / full-paper scopes presuppose that the judge really is restricted to the supplied pages.
The paper's own data hint that this confound may be present. Appendix E.4 specifically examines whether judges favor answers produced by models from their own family, which shows that the memorization/familiarity dimension was recognized — but only the model-family half was examined, not the source-paper half.
One concrete lead. Figure 1 and the worked examples in all three judge prompts are built on highly prominent public benchmarks such as MedQA / MedMCQA, and assume that "swapping the two benchmarks' scores" is a mistake models readily make. Those benchmarks are themselves in the training corpora of the models under evaluation. Does the authors' actual data contain instances of the same kind — errors a model would not make precisely because it is too familiar with the material? This bears directly on how the data were constructed: answers were generated by relatively recent models with naturally occurring errors, so if the generators are overly familiar with such background knowledge, the error distribution may not represent failure modes in real use. I would ask the authors to characterize the relationship between error types and how well known the source papers are.
W3 Further disclosure on annotation quality, and the scalability of the pipeline
The annotation quality is on the better end for work of this kind (role κ = 0.792–0.810, dependency F1 = 0.818–0.878, grounding pairwise κ = 0.839; grounding labels assigned entirely by humans without LLM pre-annotation; at least two independent annotators per paper, with rationales and evidence boxes; roughly 165 person-hours). The points below are requests for additional disclosure rather than a challenge to data quality.
First, the extent of disagreement and how it was resolved are under-reported. The paper reports agreement metrics but not the disagreement rate (how many of the 2,737 sentences reached the resolver interface), nor the proportion that remained unresolved after discussion, nor how often annotators used an override. Appendix G (Figures 15–17) describes disagreement as resolved by two annotators discussing and then selecting or overriding a label, with no third-party adjudication, so the reliability of the final labels on disputed cases cannot be assessed from the material provided.
Second, and more importantly, agreement on the INVALIDSUPPORT subset is not reported separately. The overall κ = 0.839 covers all sentences, but INVALIDSUPPORT has the longest decision chain — the role, the dependency edges, and the premise sentence's label must all be correct, and a difference in any one of them changes the final label. Appendix A already describes the reference dependency graph as "validated silver annotations" (pre-annotated by two Gemini runs, with human involvement only where the two runs disagree; its agreement with humans, κ = 0.770, is below the human–human 0.81). If the 148 INVALIDSUPPORT sentences had notably lower initial agreement between annotators than the corpus average, a substantial share of the paper's central claim — that models struggle to identify INVALIDSUPPORT — would be attributable to annotation noise.
Third, on scalability. The annotation budget is roughly 165 person-hours for 45 papers and 257 QA pairs, and grounding labels depend heavily on expert human judgment, with LLMs involved only in structural pre-annotation. This cost structure makes it hard to expand data scale and domain coverage together, which compounds the coverage issue raised in W2. This is not a defect of the paper so much as a request that the authors discuss more explicitly in Limitations what the scaling path would be if the benchmark were to cover additional disciplines.
Questions for authors
- Could the authors report the sentence-level distribution of all error codes (counts for C1–C3, N1–N3, C4, and N4, broken down by the three evidence scopes), and re-report INVALIDSUPPORT F1 split by C4 versus N4? This requires no re-inference; the existing annotations and predictions suffice.
- Could the authors provide a 2×2 decomposition: for each gold INVALIDSUPPORT sentence, cross-tabulate whether the model judged the sentence's premises (
depends_on) correctly against whether the model correctly labeled the conclusion as INV. This separates two distinct failures directly — not recognizing a bad premise at all, versus recognizing it but failing to propagate it to the conclusion. If the latter accounts for only a small share, the paper's claim that dependency reasoning constitutes a distinct bottleneck would have direct support; otherwise the claim needs revision. - Could the authors release the full list of the 45 source papers (with titles and publication years), and recompute the main metrics grouped by whether the source paper is likely to appear in pretraining data (for instance by publication year: older conference papers vs. newer 2025–2026 papers)? This requires no new annotation, but it would directly test whether the current numbers are inflated by memorization.
- Could the authors report the disagreement rate (number and share of sentences reaching the resolver), the frequency of overrides, and inter-annotator agreement specifically on the INVALIDSUPPORT subset (κ or raw agreement rate)?
6 comments
Additional analysis. Most of MMSciFact comes from recent work: 24 of the 45 source papers were published in 2025–2026, and they account for 157 of the 257 QA pairs (61%). To check whether familiarity with older papers affects the results, we split the benchmark by publication year: 21 papers published before 2025 (100 QA pairs) and 24 published in 2025–2026 (157 QA pairs). The table reports macro-F1 and INVALID SUPPORT F1 for each group across the same 12 judges (higher is better). Independent verification has no INVALID SUPPORT label, so its INVALID SUPPORT F1 is not defined.
| Setting | Macro-F1: older / newer | INV F1: older / newer |
|---|---|---|
| Independent | 0.506 / 0.473 | – |
| Holistic | 0.384 / 0.357 | 0.164 / 0.119 |
| Oracle-assisted | 0.400 / 0.373 | 0.247 / 0.207 |
Scores are slightly higher for older papers, but detecting INVALID SUPPORT remains difficult in both groups, and the reference graph improves it by a similar amount (+0.083 for older and +0.088 for newer papers). The pretraining data of the judges are not public, so no one can verify whether a paper was seen during training, and methods that test whether a text was in the training data perform close to random guessing on LLMs in most settings (Duan et al., 2024). Differences in topics or questions could also explain the gap, so we cannot attribute it to memorization. Like other benchmarks built on public scientific papers (Li et al., 2024; Wang et al., 2025a), MMSciFact limits this risk with newly created instances and mostly recent papers. We are adding this analysis and its limitations to the manuscript, along with the full list of source papers.
Further disclosure on annotation quality, and the scalability of the pipeline.
Disagreement resolution. At least two human experts independently labeled each QA pair. Of the 2,737 sentences, 301 (11.0%) received different initial grounding labels. All disagreements were resolved through discussion. No cases remained unresolved, and annotators did not use the interface's override function. Before adjudication, mean pairwise agreement was κ = 0.839. Agreement specifically for INVALID SUPPORT was κ = 0.72. We are adding these results to the annotation section.
Structural annotations. Two independent Gemini runs proposed sentence roles and dependencies. We automatically accepted the annotations when both runs agreed on the role and the complete dependency set (86%). Human annotators resolved the remaining 14%. When compared with human annotations, automatically accepted structures achieved κ = 0.770 for roles and F1 = 0.840 for dependencies. These results are close to human–human agreement (role κ = 0.792–0.810, dependency F1 = 0.818–0.878, Table 2). Human annotators also checked the dependency paths of all 148 INVALID SUPPORT sentences.
Scalability. Annotating grounding, sentence roles, dependencies, and evidence locations required about 165 person-hours from 12 ML/NLP researchers. We used LLMs to help with structural pre-annotation, but all grounding labels were assigned by humans. Expanding MMSciFact to other scientific fields would require experts in those fields, possibly using the same two-run pre-annotation approach. We are making this limitation clearer in the manuscript. The annotation guidelines and interface are also available to support future extensions.
References
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Duan, M. et al. (2024). Do Membership Inference Attacks Work on Large Language Models? COLM 2024.
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Li, C. et al. (2024). M3SciQA: A Multi-Modal Multi-Document Scientific QA Benchmark for Evaluating Foundation Models. Findings of EMNLP 2024.
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Wang, C. et al. (2025). SciVer: Evaluating Foundation Models for Multimodal Scientific Claim Verification. ACL 2025.
Thank you for your response; I have no further questions at this stage. Regarding the dataset, have you considered making it open-source? This might influence how I adjust my rating later on.
Thank you for your review!
Thank you for the careful feedback. We have completed the additional analyses described below. We are also updating the manuscript to include these results and clarify the main findings. We will upload the revised version separately.
Of the 148 INVALID SUPPORT sentences, 124 (83.8%) are C4 (a contradicted premise) and 24 (16.2%) are N4 (a premise that cannot be verified). Across the 12 judges, recall is 35.3% for C4 and 13.4% for N4. We report recall because judges predict only INVALID SUPPORT, not C4 or N4 separately. This means that false positives cannot be assigned to either type. N4 is harder to detect, but C4 accounts for about 80% of missed INVALID SUPPORT cases. The low scores therefore cannot be explained mainly by NEI premises.
We checked whether each judge correctly identified at least one incorrect premise (CON or NEI) in a conclusion's full reference dependency chain, and whether it correctly labeled the conclusion INVALID SUPPORT. This covers 1,776 judge–sentence pairs (12 × 148).
In 91.2% of missed INVALID SUPPORT cases (1,104/1,210), the judge also failed to correctly label any incorrect premise. This shows that checking the premises is a major difficulty. Even when a judge correctly labeled at least one incorrect premise, it still missed INVALID SUPPORT in 19.6% of cases (106/542). Finding an incorrect premise is therefore not enough. These 106 errors have two possible causes: the judge did not carry the premise error over to the conclusion, or it checked the conclusion itself incorrectly and labeled it CONTRADICTED or NEI, although the conclusion is supported when checked in isolation.
For the four judges tested with self-predicted graphs, the dependency linking an INVALID SUPPORT conclusion to its faulty premise was correctly identified in only 51–61% of cases. Some INVALID SUPPORT errors remained even when the dependency and an incorrect premise label were correct, although the number of such cases was small.
These analyses show that many missed INVALID SUPPORT cases come from incorrect premise labels, but two other errors also play a role: the judge does not find the dependency between the conclusion and its premise, or it finds the premise error but still gives the conclusion a wrong label. We took these findings into account when interpreting the Oracle-graph results. To know which sentences are the premises of each conclusion, we always used the human-annotated graph, also for judges that did not receive it in their prompt.
Domain coverage. MMSciFact mainly covers computer science. We do not claim that our findings apply equally to all scientific fields. Expanding the benchmark would require annotators who understand those fields. We are updating the abstract, main text, and limitations to make this scope clearer.
Pretraining familiarity. We agree that a judge may have seen a source paper during training and could rely on memory instead of the pages provided. This could also make the difference between single-page, cross-page, and full-paper evidence less clear. A judge that remembers the paper can use content from pages it was not given, so a single-page instance may in practice be checked with knowledge of the whole paper. We are adding this limitation to the manuscript. Our questions, answers, and labels are new, but that does not mean the source papers are unknown to the models. The MedQA/MedMCQA error in Figure 1, for example, appeared naturally in a generated answer. We did not introduce it ourselves.