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Under review as a conference paper at ICLR 2027

Valid but Wrong: Decomposing Language-Model Errors on Closed Vocabularies

Abstract

Practitioners repair language-model output by sampling more, saying more in the prompt, or constraining the decoder. We ask which lever fixes which error, on a task family where the answer is measured exactly: generation against a closed vocabulary, where a machine-checkable oracle separates syntactic error, membership error (hallucinated terms), choice error (wrong real terms), and assembly error (wrong structure). Across more than twenty scored conditions, spanning an intervention ladder on a primary ontology, a cross-ontology validation on a second, and three frontier model tiers, the classes behave in opposite ways. Repeated sampling drives coverage of syntactically valid output to by , while coverage of even half-correct term choice is zero in samples. Constrained decoding raises membership to but degrades structure (paired assembly delta ), and its naive greedy form collapses into repetition loops. A validator repair loop recovers membership () yet lifts choice only to ; a retrieval-only solver peaks at . The strongest condition we find, a frontier model with the vocabulary and per-term descriptions in context, reaches choice , and the same condition on a bijectively renamed vocabulary the model has never seen reaches : familiarity from pretraining is worth (95% CI ), and binding novel symbols to in-context definitions recovers the rest, though replacing meaningful identifiers with arbitrary ones changes more than familiarity alone. Every intervention we test leaves this term-selection residual largely intact; high conformance systematically hides it. In the Linked Open Vocabularies catalogue, 56% of 529 parsed ontologies declare zero refutation-enabling axioms, so for the catalogue's parseable half, even the conformance side of such an oracle is typically unavailable.

Primary area:
datasets and benchmarks
Keywords:
structured generation, constrained decoding, error decomposition, evaluation, hallucination, tool calling, knowledge graphs, ontologies, test-time compute, data contamination

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_eq6vOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

The paper is a survey on the effects of various methods in the setting of generation against a fixed ontology. The three evaluation datasets are OOD-100, and Strict-20, each containing items encoded in IES4 and Biolink, respectively. The authors test and analyze a few methods, including a greedy generation baseline, a best-of-N sampling, trie-based constrained decoding, etc... and measure many metrics including syntax validity, membership rate, and the overall metric F1choice−allF_1^{choice-all}. The authors report a subset of these metrics on one dataset, and then go on to analyze the effect of a few methods and detail their limitations in the subsequent sections.

Critical strengths

None

Critical weaknesses

My concern is that this paper contains a large amount of LLM generated text. None of the datasets or metrics are explicitly defined in text (only using plausible sounding vocabulary such as syntax validity, membership rates, F_1 score). Moreover, there are many formatting errors and inconsistencies between the descriptions.

Major issues (a small subset).

  • No (high-level) description of the task / any examples. What are the IES4 and Biolink ontologies? What are the OOD-100 and Strict-20 datasets? [103-107]
  • No concrete description of the metrics. The metrics included involve "syntactic validity, membership, choice F1F_1, and F1choice−allF_1^{choice-all}" [119]. How are each measured? The text mentions that all generations are possible as per some "system" [137], what is this system? What are the definition of some terms: "canonicalisation slack" [142] "entailment-reduced variant" [141]?
  • Models. What are the "frontier arms [that] run three tiers of one commercial family"? [153] What is the "open 30B MOE coder model" used by the local family [155]. What is a "3B floor check model? [155] What purpose does it serve and where are the results of this floor?
  • Methods. No description at all of the methods outside of a brief one line description. How are you forming the "plain validator loop" [169] or doing "constrained decoding" [170]. No details contained in appendix at all.
  • Findings. The findings indicate that the best performing model is just a frontier model (where are the other tiers?) with the vocabulary in context? What should I take away from this?
  • BoN sampling. Why is this a separate table? What intervention is this BoN on? [188]
  • Biolink. Where are the results for this? These results are mentioned on line 353 but never shown in text or appendix.
  • Formatting issues. All the section headers and titles break format convention.
Questions for authors

n/a

Reviewer_gRUoOpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies closed-vocabulary generation: a model reads a natural-language scenario and encodes it as RDF Turtle using only the terms of a given ontology. The primary ontology is IES4, a UK government standard with 714 terms. Replications use Biolink, a non-template IES4 set, and tool calling over the GitHub REST API.

The authors run an intervention ladder on a 30B model and on three frontier tiers. Sampling, constrained decoding, in-context vocabulary, and validator loops all raise membership to 0.75 or higher, but choice F1 stays at 0.45 for the local model and 0.78 for the frontier model. A renamed clone of the vocabulary bounds the pretraining-familiarity effect at 0.08. One in-family worked example lifts the 30B model to 0.95. The authors conclude that the residual is missing knowledge of the ontology's modelling conventions. A census of 529 public ontologies finds 56% with no constraint axioms. For most deployed vocabularies, the oracle used here does not exist.

Critical strengths

The paper is easy to follow. The renaming experiment in Section 5 is well designed. Every term is replaced by an arbitrary six-letter code, the glossary is held fixed, and the largest Claude tier loses about 0.08 in choice F1 (Table 2). Given how long IES4 has been public, I'd have expected memorization to be worth more than that. The effect is smaller but present on a second model family. The follow-up condition, in which plausible English pseudonyms score below the arbitrary codes, is the part of the experiment I found most informative.

Critical weaknesses

This is schema linking measured on RDF, and the result is known in the text-to-SQL literature. The task is narrow, the four-class error decomposition is a rule-based scorer, and the pattern (sampling repairs syntax, constrained decoding and vocabulary in context repair membership, and the term-choice gap stays mostly open under all of them) is what schema-linking work on text-to-SQL has reported for years. The introduction says as much, describing the phenomenon as "recognizable as schema linking under a large candidate set", and locates the novelty in measuring which intervention moves which error class. I don't think a more precise measurement of an expected pattern is enough for ICLR. The bibliography contains no text-to-SQL work at all: Lei et al. (EMNLP 2020, https://aclanthology.org/2020.emnlp-main.564/) already put schema linking at the centre of text-to-SQL error analysis, RESDSQL (Li et al., AAAI 2023, arxiv.org/abs/2302.05965) decouples it from skeleton parsing much as this paper separates choice from assembly, and the synonym-renamed condition in Section 5 is close to the schema-synonym perturbation in Dr.Spider (Chang et al., ICLR 2023, arxiv.org/abs/2301.08881). For the decoder, trie-constrained generation over a closed vocabulary is GENRE (De Cao et al., ICLR 2021, arxiv.org/abs/2010.00904) and GenIE (Josifoski et al., NAACL 2022, arxiv.org/abs/2112.08340); the paper cites the grammar-constrained decoding line but neither of these. Given that literature, the paper reads to me as an experiment report that confirms a known effect on RDF. The benchmark, the scorer and the LOV census in Section 7 would be of more value to the knowledge-graph or semantic-web community than to this venue.

With vocabulary in context, the 30B model's choice F1 on the GitHub API goes from 0.41 to 0.94. On Biolink the same intervention produces no measurable change. The paper explains both through familiarity: every model has seen GitHub, so access to the vocabulary nearly closes the gap, and Biolink's membership is already high, so there is nothing for the vocabulary to repair. That reads as post hoc to me, and the paper gives no way to test it. Biolink's absolute choice level is never reported, only the paired delta, so whether a familiar schema in fact has a high choice ceiling can't be checked, and no second schema with low pretraining coverage is tried. The low ceiling may simply be a property of IES4.

Questions for authors
  1. The related-work section states that "renaming a real 1,220-operation vocabulary preserves schema realism while breaking memorization", but Section 6 reports no renamed-GitHub arm. Was such an arm run? If so, please report it (see Weakness 2).

  2. Would be more informative if the absolute choice F1 on Biolink for each arm is reported as Table 1 does for IES4.

  3. Beyond the schema-linking literature, what does this paper establish that was not already known?

Reviewer_JhZbOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies structured generation over closed vocabularies, separating evaluation into syntactic validity, vocabulary membership, term choice, and structural assembly. It compares sampling, contextual information, constrained decoding, and validator-based repair. The main finding is that improvements in conformance do not necessarily translate into comparable improvements in semantic correctness.

Critical strengths
  1. The paired intervention experiments make the evaluation decomposition practically useful: they show which aspects of output quality each intervention improves. For example, constrained decoding raises membership from 0.179 to 0.969, while choice F1 reaches only 0.283.
  2. Renamed-vocabulary experiments and in-family demonstrations provide useful diagnostic controls for investigating familiarity and access to modelling conventions.
  3. Cross-ontology and tool-calling evaluations help assess the scope of the observations, while the reported scorer defects and rescoring procedure demonstrate attention to evaluation reliability.
Critical weaknesses

The main concern is that the experiments do not fully distinguish limitations in model capability from insufficient specification of the required modelling conventions. A single in-family example raises choice F1 to 0.946 for the 30B model and 0.995 for the largest frontier model. This is informative, but it remains unclear whether the example supplies missing rules, enables template imitation, or teaches transferable conventions. The authors acknowledge this distinction and treat the in-family condition as calibration. Nevertheless, some broader claims about the persistence of the term-selection residual appear stronger than the evidence supports. The decomposition and observed intervention effects are useful; the explanation of the remaining errors is less firmly established.

Questions for authors
  1. How does performance change when modelling conventions are explicitly provided as rules, without a same-family worked example?
  2. Does the benefit of in-family demonstrations transfer to novel compositions and non-template instances?
  3. Could the conclusions more clearly distinguish the observed residual under the tested information conditions from a broader limitation of model capability?

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