acceptodds
Under review as a conference paper at ICLR 2027

When Are Tool Calls Necessary? Counterfactual Evaluation and Pre-Generation Epistemic Gating in Tool-Augmented Language Models

Abstract

When a tool-augmented language model outperforms its closed-book counterpart, the improvement is routinely credited to external computation or retrieval. We show that standard evaluations conflate two effects: the information a tool provides (Non-Parametric Information Gain, NPIG) and the effect of switching to a protocol in which the model must format a tool call before answering (Structural Scaffolding Effect, SSE). To separate them, we introduce an 8-Arm Counterfactual Matrix that holds Turn-1 tool calls byte-identical across real execution, self-simulation, schema-echo, empty return, and adversarial conflict. On solvable parametric tasks, action-first JSON calling lowers accuracy below closed-book answering. The largest group of lost items has a valid call but no checking after the tool returns (Stage-2 Post-Call Deliberation Suppression); smaller groups have call arguments corrupted before reasoning (Stage-1 Premature Schema Compression) or no call at all. Control experiments show that the loss is not caused by showing tool schemas or by our echo wording: it appears once a call is required, persists with neutral echo text, native tool templates, and grammar-constrained JSON, and mostly disappears when the model is asked to verify its answer after the tool returns. In a 40-item-per-benchmark study across 12 SOTA datasets with a local lookup/solver tool, an oracle that returns the gold answer on every call gives 29.9 percentage points higher accuracy than real execution; on the calls that return the gold answer, text LLMs jump by 55.7 percentage points over an echo (), whereas Qwen2.5-VL () already reads the answer from the image closed-book and barely changes across real, echo, or empty returns. Finally, our truncation-corrected entropy () predicts closed-book errors on lookup tasks, but requires per-task calibration and does not beat simpler prefix scores on actual tool benefit; when tools are fallible, prefix uncertainty is near chance and our passive 90-feature Logit-Lens probes fall to chance on unseen models and benchmarks.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Tools, Tool Calling, LLM, Machine Learning, Artificial Intelligence, Natural Language Processing, tool-augmented language models, AI agents, causal mediation analysis, epistemic uncertainty quantification, tool necessity, counterfactual evaluation, routing and gating

Reviews

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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_NTo7OpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
1
Soundness
2
Read review
Paper summary

This paper studies when language models actually benefit from external tool calls and whether existing evaluations correctly measure those benefits. The authors introduce an eight-arm counterfactual evaluation framework to separate improvements caused by external tool information (NPIG) from changes introduced by the tool-calling protocol itself (SSE).

The paper also identifies several failure modes in tool-augmented reasoning, including premature argument generation and reduced verification after tool execution. Additionally, it investigates whether uncertainty estimates and hidden-state probes can predict when tools are needed.

Experiments across multiple models, controlled tasks, and 12 benchmarks show that requiring tool calls can hurt performance on tasks that models could otherwise solve internally. The authors also find that simple uncertainty-based routing methods struggle when tools are unreliable, while hidden-state probes fail to generalize to unseen models and benchmarks.

Critical strengths

1- The paper addresses an important question that is often overlooked in tool-augmented LLM evaluation: whether improvements actually come from external information or from changes in the interaction protocol. The proposed counterfactual framework is useful because it compares different tool responses while keeping the initial tool call fixed. This provides a more informative evaluation than simply comparing tool-augmented and closed-book accuracy.

2- The authors evaluate several models, benchmarks, and tool-calling configurations. The experiments include meaningful controls for prompt formatting, tool execution, and uncertainty-based routing. I particularly appreciate the finding that valid tool calls do not necessarily lead to better final answers, as well as the analysis showing that hidden-state probes can perform well in-distribution but fail under distribution shift. These observations provide useful insights for designing and evaluating tool-using agents.

Critical weaknesses

1- Although the counterfactual evaluation framework is useful, the underlying decomposition is largely based on differences between experimental accuracies, and the proposed entropy correction follows directly from Shannon's grouping identity. The methodological novelty therefore seems more empirical than theoretical. More importantly, the conclusions rely heavily on the selected tool-calling protocols. The main experiments use relatively restrictive action-first JSON calls and local deterministic tools, which may not represent how modern reasoning agents interact with external tools. The paper itself shows that alternative prompting and action formats can substantially change performance. Also, the proposed failure taxonomy does not fully establish the underlying mechanisms. For example, classifying an incorrect answer after a valid tool call as post-call deliberation suppression does not necessarily prove that the model stopped reasoning or verifying its answer. These concerns limit how broadly the findings can be interpreted.

2- Although the experimental evaluation is extensive, some important conclusions are based on relatively small or restricted settings. Suite II uses only 40 examples per benchmark and a generic local tool, while the visual-language findings are limited to one model family and a small number of gold-return cases. The oracle experiment also provides the correct answer directly, making its large advantage over real execution an optimistic upper bound rather than a realistic estimate of available tool improvements. Furthermore, the proposed entropy-based gate does not consistently outperform simpler uncertainty measures on actual tool benefit.

3- Almost all the main tables use extremely small fonts, making their values difficult to read without significant zooming. Many paragraphs are unnecessarily long and packed with numbers, equations, abbreviations, and statistical results. For example, the Pitfall 2 paragraph on page 8 contains numerous percentages, sample sizes, confidence intervals, and comparisons in a single dense paragraph, making the main finding unnecessarily difficult to understand. Even several table and figure captions are excessively long and contain extensive experimental details that would be better explained in the main text. The paper would benefit significantly from larger tables, shorter captions, simpler paragraphs, and a clearer separation between the main findings and supporting numerical details. The current presentation makes the paper much harder to follow than necessary.

Questions for authors

1- How well do the findings extend to more realistic tool-using agents, particularly those using native function calling, interleaved reasoning, or multi-step interactions? Since the paper shows that action formatting affects performance, additional experiments with more representative agent configurations would help establish the generality of the conclusions.

2- How do the authors distinguish actual post-call deliberation suppression from other reasons a model might produce an incorrect answer after a valid tool call? Can this mechanism be validated more directly, rather than inferring it primarily from tool-call validity and final-answer correctness?

3- How representative are the local solve-or-lookup tools of real tool-augmented applications? Also, can the authors evaluate whether the main conclusions hold with larger benchmark samples, more diverse tools, and additional VLM families? This is particularly important for the text-versus-VLM comparison in Pitfall 2.

4- Since simpler uncertainty measures perform comparably or better on actual tool-benefit prediction, what is the practical advantage of using the proposed corrected entropy? Can the authors demonstrate improvements under stronger held-out transfer settings without requiring task-specific threshold calibration?

Reviewer_ntDjOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper studies when tool calls are necessary for LLMs and how tool calling affects model performance. The authors propose an 8-arm counterfactual evaluation framework to separate the effect of tool-calling process from the information provided by tools. They also investigate different failure cases during tool calling and propose an uncertainty-based gating method to decide whether a model should use tools. The experiments show that requiring tool calls can sometimes reduce accuracy, while the benefit of using tools depends on the information they provide.

Critical strengths

None

Critical weaknesses
  1. The paper mainly identifies the Stage-2 deliberation suppression based on the echo setting, where the tool does not provide useful information. However, the performance drop may also be caused by the unusual tool responses, instead of the model reducing its reasoning. Also, the verification instruction improves accuracy in the echo setting, but reduces accuracy by 2.4 percentage points with real tools. This makes it unclear whether the finding can generalize to real tool-using systems.

  2. The closed-book accuracy in Suite II is much lower than previously reported results on several benchmarks. Although the authors acknowledge this limitation, it is unclear whether the experimental setting can reflect the actual model performance. Since several main findings are based on this setting, the generalizability of these results is questionable.

Questions for authors
  1. Why does the verification instruction improve performance in the echo setting but reduce accuracy when using real tools? Can the authors provide more analysis to explain this difference?

  2. Can the authors explain why the closed-book accuracy in Suite II is much lower than previously reported results? Have the authors considered testing with different prompts or generation settings to see if the main conclusions still hold?

Reviewer_LNKnOpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates when tool calls benefit language models, distinguishing the contribution of external tool outputs from the effects of the tool-calling protocol itself.

The authors introduce an eight-arm counterfactual framework that holds the initial tool call fixed across five observation conditions (real execution, self-simulation, empty returns, schema echoes, and adversarial outputs), alongside closed-book, reflection, and gating baselines. They decompose total tool gain into a Structural Scaffolding Effect (SSE) and Non-Parametric Information Gain (NPIG).

Experiments across controlled tasks and text and vision benchmarks show that action-first tool calling can reduce accuracy on solvable reasoning tasks. The authors analyze failure modes, compare real and oracle tool execution, and examine the limitations of pre-generation tool routing using truncation-corrected entropy and hidden-state Logit-Lens probes.

Critical strengths
  1. Counterfactual Evaluation Framework. The proposed framework provides a useful way to disentangle the effects of tool-calling protocols from those of external tool outputs. Holding the initial tool call fixed across observation conditions enables more controlled comparisons than standard end-to-end evaluations and reveals opposing effects that aggregate accuracy can obscure.

  2. Extensive Empirical Evaluation. The paper evaluates multiple models and tasks, with targeted controls for prompt and action-format effects. Its additional out-of-distribution and shortcut analyses provide useful evidence about the limitations of uncertainty-based tool routing.

Critical weaknesses
  1. Insufficient evidence for the proposed mechanistic failure taxonomy.

The paper assigns mechanistic labels such as Post-Call Deliberation Suppression and Premature Schema Compression primarily based on Turn-1 call validity. However, call validity alone does not uniquely identify the underlying failure mechanism.

The verification and alternative-action ablations provide supporting evidence but do not fully resolve this ambiguity. In particular, the DirectCoT intervention changes both the system prompt and generation budget. Appendix Table 8 reports failure-category counts pooled across seven tasks, whereas verification-related accuracy improvements are reported for calc-reach from separate reruns. These aggregate results do not establish which original failure categories are specifically recovered. Although the more targeted B4 control provides stronger evidence for the effect of verification, it likewise does not establish category-level mechanistic attribution.

Thus, the experiments support a useful observational taxonomy more directly than the proposed mechanistic explanations. This distinction matters because explaining these failure mechanisms is presented as a central contribution.

  1. Unclear broader significance of the counterfactual diagnostic contribution.

The matched-observation framework is a useful methodological contribution, but its incremental scientific significance remains somewhat unclear. Prior work has already documented reasoning degradation under structured-output constraints and performance differences across action protocols. Although the proposed framework provides more controlled comparisons, the paper could more clearly establish which substantive new insights emerge from its counterfactual analysis beyond these previously observed effects.

The strongest negative SSE findings arise primarily under action-first structured calling, and the alternative-action experiments demonstrate substantial protocol sensitivity. Furthermore, Suite II relies on deliberately fallible local tools and reports closed-book accuracies below previously published results. While these limitations are acknowledged, they leave uncertainty about how broadly the findings extend beyond the evaluated protocols and tools.

Consequently, although the framework offers valuable diagnostic capabilities, I remain uncertain whether the findings establish a sufficiently distinct and broadly significant scientific contribution.

Questions for authors
  1. Mechanistic attribution. Can the authors provide more direct validation of the proposed Stage-1 and Stage-2 failure mechanisms beyond Turn-1 call validity? In particular, where matched verification and non-verification results are available, can they report paired, item-level recovery rates by the original failure categories and assess whether Stage-2 cases recover at a higher rate than other categories? This would help distinguish evidence for the proposed mechanisms from an observational classification of failures.

  2. Protocol dependence. How should the central negative SSE findings be interpreted in light of the substantial protocol sensitivity observed in the ReAct, CodeAct, and native-thinking ablations? In particular, which conclusions remain robust across action protocols, and which are specific to action-first structured calling? Clarifying this distinction, ideally using matched protocol comparisons, would help establish the broader significance of the findings.

  3. Incremental value of the additional counterfactual arms. Beyond the core closed-book, echo, and real-execution comparison, which central scientific conclusions depend on the additional counterfactual arms? Can the authors identify a substantive finding that would be missed or materially altered under the simpler comparison, and explain how it advances beyond existing analyses of structured-output constraints and action protocols? This would help clarify the incremental scientific significance of the full framework.

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