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Withdrawn from ICLR 2027

From Information Value to Intervention Value in Language Models

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Additional information can improve language model performance, but measuring that potential does not tell us what system change will realize it. We study the gap between the value of information and the value of interventions. We separate four questions: whether oracle information improves task utility (*opportunity*), whether the channel used to supply it preserves that gain (*instrument validity*), whether the remaining shortfall can be reliably assigned to information acquisition or use (*attribution*), and whether acting on that assignment improves utility on held out data (*decision validity*). Across eight benchmarks, oracle information value is the most robust quantity in our audits, while attribution can change under subsampling, reference construction, and reader family. On BigCodeBench, the injection channel itself destroys the oracle gain, making recovery measurements uninterpretable. We then test the final question prospectively on FEVER and QASPER. With 56 diagnostic items per system, the procedure produced stable shortfall attributions under subsampling and threshold perturbations, yet the corresponding frozen interventions reduced utility on untouched test sets by 0.078 verdict accuracy on FEVER and 0.048 QASPER score on QASPER. In both cases, another declared action performed better. These results distinguish two problems: locating where information value is lost and determining which intervention has value. They motivate a simple workflow: use the diagnostic to form intervention hypotheses, then measure intervention value directly on held out outcomes.

Primary area:
foundation or frontier models, including LLMs
Keywords:
language models, information value, intervention value, model diagnostics, oracle evaluation, retrieval augmented generation, decision validity

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_4zmBOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
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Paper summary

This paper introduces four different validity measures to distinguish between the value of information provided to a model for a specific task and the value of an intervention. The validity claims: 1) Opportunity Gap, 2) Instrument Validity 3) Attribution and 4) Decision Validity, provide different sources of signal that are used to understand the utility of information across 8 tasks with the key finding showing oracle information value being the most informative and robust compared to attribution which can change. The paper also conducts a prospective test across two datasets and shows that information value, shortfall attribution and intervention value are different quantities and should be factored in as opposed to relying on one value.

Critical strengths
  1. The paper introduces and tests the diagnostic framework across a wide range of different tasks and provides ablations across models of different sizes.
  2. The prospective test is well-grounded but could be improved in its clarity and presentation.
Critical weaknesses

W1: The significance of the framework presented in the paper in contrast to existing approaches remains unclear

Throughout the work, several different metrics that are designed to diagnose the value of information provided or the value of intervention i.e. Opportunity gap, instrument validity, attribution, decision validity, scope, regret, stability etc. It is still unclear what the overall takeaway of these metrics are and how they complement existing work that already report versions of these metrics. It is common practise in RAG benchmarks to report a no-context baseline, an oracle and a retrieval baseline. It remains unclear the significance the metrics this work introduces towards offering new insights that existing approaches already cover. How do the findings of this work translate to how we should evaluate models and how we should select intervention policies -- these questions remain open yet the work sets out to address them. Table E.1. presented in the Appendix provides no citations for any of the prior methods making it hard to do a comparison to existing approaches.

What would help address this concern? In the discussion of the findings, provide a clear explanation of how the results presented differ from existing evaluation approaches and what novel information the distinction between value of information and value of intervention provides. It is important to clarify what the new approach adds that explicitly differs from what existing approaches already report and the practical significance.

W2: Limited error analysis

The results presented on BigCodeBench are interesting but no error analysis is provided to help understand why this behaviour occurs specifically on this dataset or model and whether it generalises to other datasets of similar properties.

What would help address this concern? Beyond just providing the quantitative values for each validity, a futher analysis on BigCodeBench is needed to explain the observed invalid recovery instrument.

W3: A justification on the choice of experimental setup is lacking

The paper does not provide a principled justification as to why certain datasets were specifically used for this task. Most of the tasks used i.e. information retrieval tasks like BrowseComp, HotpotQA are designed to require retrieving from external sources hence some of the findings are not suprising i.e. BrowseComp is designed to be intentionally difficult to solve parametrically.

What would help address this concern? Provide a clear justification on the choice of tasks selected and how it potentially affects the intepretation of the results.

Questions for authors
  1. The presentation of the four validity claims can be better improved for readability and clarity. Here are a few suggestions I would make:
  • Provide a reference or a worked example to show how it relates to each metric e.g. a question from FEVER.
  • Use consistent naming of the metrics from when first introduced i.e. the headings in L124, L139 are mismatched from the claim names in Table 1, even though they are written to provide definitions. I would suggest to keep it consistent with the table.
  • Reuse notations across the different claim definitions instead of introducing new notations for the same concepts e.g. mean utility without supplied information can be standardised in both Opportunity and Instrument Validity.
  1. A clear experimental section that provides details on the choice of datasets used or models evaluated is missing. Were the datasets chosen because they have certain properties that allow you to measure the validity claims, how do you controll for datasets that models may have already been exposed to at pretraining or are saturated e.g. GSM8K, do you do an initial ablation to test for questions that models can already solve prior to providing oracle information? It is interesting to note that for I would suggest to the authors to provide a clear experimental section that provides details of the experiments. L087 - L090 provides the models used but this is misplaced in the introduction.

  2. Use consistent naming of the validity terms across the paper. Opportunity shifts to Headroom in Table 2 while uses a different naming when presented in Section 2. I also noted areas wher the term Information Gap is used to refer to Opportunity. I would suggest standardising the use of terms in the paper.

  3. Isn't the instrument validity is presented as a numeric value but reported as a binary label between VALID and REJECTED in Table 2? If so, the definition in Line 144 should be clarified to reflect the set options i.e {VALID, REJECTED}. Also in the appendix there is a lack of consistency in the usage of the labels as INVALID is now used, is INVALID and REJECTED the same thing?

  4. Are the interventions generalisable and what are is practical utility of the defined action menu beyond the tasks included in the paper?

Reviewer_C3YgOpenReview ↗
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Informativeness
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Paper summary

The paper formalizes the distinction between information value (the theoretical utility gained from an oracle, Δ=E[u(g∗)−u(∅)]\Delta = \mathbb{E}[u(g^*) - u(\emptyset)]) and intervention value (the empirical treatment effect of a system modification, τa=Ua−UNOOP\tau_a = U_a - U_{\text{NOOP}}). The authors decompose this transition into four sequential validity claims: (1) Opportunity, (2) Instrument Validity, (3) Attribution, and (4) Decision Validity. Auditing eight benchmarks with Qwen-series models, the paper highlights that teacher-forced measurement channels can invalidate oracle gains (e.g., on BigCodeBench), self-recovery realization consistently collapses (Rself≈0R_{\text{self}} \approx 0), and shortfall attributions can be unstable across references. In a prospective evaluation on FEVER and QASPER (n=56n=56 each), frozen attribution mappings select interventions that yield negative treatment effects on held-out test splits (τ=−0.078\tau = -0.078 and −0.048-0.048), trailing an un-diagnosed reader upgrade.

Critical strengths
  1. The four-stage framework clearly delineates where diagnostic pipelines break down, providing rigorous mathematical definitions, explicit undefined-state semantics, and regret pricing for abstentions.
  2. The BigCodeBench analysis effectively proves that teacher-forced measurement channels can actively destroy oracle gains (0.273→0.1030.273 \to 0.103), providing a valuable sanity check that prevents misinterpreting zero-correlation diagnostic signals.
  3. The authors commendably document negative outcomes, including protocol deviations on QASPER (L362–366), an un-run control arm (CTRL_SAMPLE), high nonpositive bootstrap denominator rates (46.6%), and non-reproducible historical BIRD baselines.
  4. The diagnostic audit spans eight diverse benchmarks across code, multi-hop QA, and SQL generation, supplemented by reader-family sensitivity checks (Llama, Gemma) and scaling analyses up to 14B parameters.
Critical weaknesses
  1. The paper’s headline conclusion, that a stable shortfall attribution does not guarantee a positive interventional treatment effect, follows directly by construction. Oracle attribution measures theoretical headroom under perfect information (g∗g^*), whereas τa\tau_a evaluates an imperfect, noisy algorithmic implementation against an arbitrary menu. Because nothing in the mathematical formulation connects diagnostic stability to treatment efficacy, showing that an imperfect intervention degrades performance is not surprising. Without empirical prevalence estimates or a predictive model linking attribution severity (1−Rret1 - R_{\text{ret}}) to treatment rank across many systems, two isolated counterexamples provide limited insight.
  2. The prospective validation on QASPER is compromised by an execution discrepancy: the freeze-commit table designated acquisition, yet the executed evaluation deployed self-recovery (L362–366). Crucially, an outside-menu BM25 acquisition intervention achieved τ≈+0.139\tau \approx +0.139 (App. C.2), beating all menu actions, including the reader (+0.036). Had the registered acquisition action been executed, the diagnostic would have successfully selected the optimal action, invalidating QASPER as a failure case and leaving the paper with only n=1n=1 compliant counterexample.
  3. On FEVER, the mapped acquisition intervention degraded accuracy (τ=−0.078\tau = -0.078). However, the retriever architecture, top-kk, and evidence hit rates are completely omitted. Distractor-induced degradation in small (3B) models is well-documented; noisy retrieval frequently degrades claim-only priors. Tellingly, an outside-menu self-evidence generation baseline achieved τ≈+0.299\tau \approx +0.299, demonstrating that this model strongly benefits from evidence when properly formatted. The failure appears to be an artifact of an under-tuned retriever rather than a breakdown of acquisition as an interventional target.
  4. The finding that Rself≈0R_{\text{self}} \approx 0 across all tasks likely reflects the mechanics of teacher-forcing rather than an intrinsic model limitation. Forcing self-generated tokens through a teacher-forced channel reproduces free generation by construction, driving Rself→0R_{\text{self}} \to 0 whenever uˉ∅≈uˉfree\bar{u}_\emptyset \approx \bar{u}_{\text{free}}. Furthermore, the paper's own data contradicts this claim:
  • On BIRD, baseline $\bar{u}_\emptyset $ shifts between 0.163 and 0.179 across sections, implying Rself≈−0.18R_{\text{self}} \approx -0.18.
  • Figure G.1 (right) displays self-recovery realization between −0.45-0.45 and −0.30-0.30.
  • On SciFact, RselfR_{\text{self}} reaches 0.9690.969 (Table B.6).
  1. Table 3 reports point estimates for treatment effects (τ\tau) without confidence intervals, standard errors, or hypothesis tests, despite defining a paired bootstrap in the appendix. On QASPER (n=285n=285), standard errors are roughly ±0.02\pm 0.02, leaving it statistically ambiguous whether the reader's gain (τ=+0.036\tau = +0.036) is distinguishable from NOOP. Furthermore, subsampling within a fixed sample of n=56n=56 cannot detect distribution shifts between diagnostic and test splits.
  2. Inconcistencies:
  • BIRD Δ\Delta Discrepancies: The text reports four conflicting values: 0.1180.118 (Table 2), 0.1200.120 (Fig. B.1a), ≈0.09\approx 0.09 (L1265), and 0.0920.092 (Δinstr\Delta_{\text{instr}}).
  • Component Headroom Paradox: In Fig. B.1b, value-only (+0.182) and schema-only (+0.125) lifts each individually exceed the full gold lift (0.118).
  • Correlation Mismatches: L1269–1271 reports cross-domain Kendall τ\tau between BIRD and QA tasks as "near zero," whereas Fig. G.3b displays values of −0.67-0.67 and +1.00+1.00.
Questions for authors
  1. What was the explicit implementation specified for acquisition in the freeze-commit table? What is its realized τ\tau on final_test, and how does it compare to the outside-menu BM25 result (τ≈+0.139\tau \approx +0.139)?
  2. What specific retriever, embedding model, index, and top-kk were used for FEVER acquisition? What was the gold-evidence recall@kk, and what is τ\tau when evaluated strictly on instances where gold evidence was retrieved?
  3. How do you separate the finding of Rself≈0R_{\text{self}} \approx 0 from the mechanical tautology of teacher-forcing self-generated outputs? What are the exact values of RselfR_{\text{self}} and RretR_{\text{ret}} for the n=56n=56 FEVER and QASPER diagnostic splits?
  4. What are the 95% bootstrap confidence intervals and P(a=a∗)P(a = a^*) values for each τa\tau_a in Table 3? Is the reader gain on QASPER statistically distinguishable from zero?
  5. Why do isolated schema and value groundings in Fig. B.1b produce larger utility gains than the combined full oracle grounding?
Reviewer_y4qhOpenReview ↗
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2
Confidence
3
Informativeness
3
Presentation
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2
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Paper summary

This paper studies the distinction between information value, shortfall attribution, and intervention value in language model systems. It separates four evaluation stages: whether oracle information improves utility, whether the information-delivery channel preserves that benefit, whether unrealized value can be reliably attributed to a particular shortfall, and whether an intervention selected from that attribution improves held-out utility.

Across eight benchmarks, the authors find that information opportunity is generally more robust than shortfall attribution. They also identify a BigCodeBench setting where the recovery measurement channel destroys the oracle benefit. In prospective experiments on FEVER and QASPER, the selected actions remain stable under the tested perturbations but reduce held-out utility relative to NOOP by 0.078 and 0.048, respectively. QASPER has a disclosed action-menu deviation. The main contribution is a framework separating diagnostic evidence from intervention value, supported by cases where stable diagnoses map to harmful actions.

Critical strengths

1.The research question is clear and practically relevant. Oracle comparisons are a natural tool for diagnosing information-augmented systems. Testing whether these diagnoses support concrete engineering decisions addresses an important practical question.

2.The framework makes useful distinctions. Separating information opportunity, channel validity, attribution stability, and intervention value helps clarify what each experiment establishes. The BigCodeBench channel check provides a concrete example where the measurement procedure itself undermines the interpretation of recovery metrics.

3.The prospective design includes valuable safeguards. The diagnosis-to-action mapping is frozen before test outcomes are observed, and the selected action is compared with NOOP, alternative interventions, and fixed policies. The selected actions remain worse than NOOP when the reader intervention is excluded, so their negative effects are not solely an artifact of comparison with a stronger reader.

4.The reporting is appropriately transparent. The authors disclose the QASPER protocol deviation, distinguish prospective evidence from interventions developed after inspecting diagnostics, and avoid interpreting two cases as an estimate of failure prevalence.

Critical weaknesses

1.The experiments do not sufficiently establish that the targeted interventions improve the diagnosed components. On FEVER, the acquisition intervention performs full-corpus retrieval and supplies the resulting evidence to the reader. However, the paper does not sufficiently demonstrate whether this action improves evidence recall, precision, or another relevant acquisition metric relative to the original system. Consequently, the negative effect could reflect an inadequate diagnosis-to-action mapping, or simply an intervention that fails to repair the targeted component. The evidence supports the narrow conclusion that this frozen mapping selected a harmful action, but provides limited explanation of whether the failure originates in attribution, action selection, or implementation. The authors appropriately acknowledge that intervention failure does not establish component irrelevance, but this also highlights the need for stronger mechanism analysis.

2.Uncertainty reporting is insufficient for the central intervention effects. Table 3 provides confidence intervals for the diagnostic Information Gap, but not for the two central negative intervention effects or operational regret. This is particularly important for QASPER, which has only 285 test items. The scoring procedure and statistical unit should also be specified. If multiple questions come from the same paper, the analysis should explain how within-paper dependence is handled.

3.The diagnostic rules and intervention configurations are not sufficiently specified in the PDF for independent reconstruction. Appendix A.3 uses descriptions such as “sharp acquisition shortfall,” but does not fully specify the numerical attribution rules, how competing shortfalls are resolved, or the subsample sizes and threshold perturbation ranges used in the prospective stability tests. Important implementation details, including intervention prompts and sampling aggregation rules, are also insufficiently documented. These details may exist in the separate supplement, but the submitted PDF alone does not make the central procedure independently verifiable.

4.The connection between self-recovery measurements and component attribution needs clarification. Low self-recovery realization can reflect missing factual knowledge, incorrect intermediate-information generation, representation mismatch, or downstream utilization difficulties. It does not independently identify a utilization bottleneck. Although the paper often uses the more cautious term “self recovery,” it should clarify which component-level interpretations these descriptive measurements support.

5.The incremental empirical insight remains limited. The observation that stable attribution does not guarantee effective intervention is reasonable and useful. A reliable counterexample is sufficient to reject a universal guarantee; therefore, a large task collection is not necessary for that logical claim. However, the current results provide limited insight into when such failures occur, why they occur, or under what conditions diagnostics remain actionable. The QASPER menu deviation further weakens the second case as confirmatory evidence.

Questions for authors

1.Does the FEVER acquisition intervention demonstrably improve retrieval quality? Please report evidence recall and precision before and after intervention, and relate these changes to downstream correctness.

2.What are the paired confidence intervals for the central intervention effects? How are QASPER scoring, the statistical unit, and within-paper dependence handled?

3.Can the authors provide the complete attribution rules and the subsampling and threshold-perturbation configurations underlying the reported stability of 1.00?

4.Can anonymized preregistration records and code versions verify the chronology of the QASPER menu deviation and clarify its implications?

5.Are there existing results for another reasonable intervention targeting the same diagnosed shortfall that could help distinguish component-selection failure from implementation failure?

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