- Rating
- 2(+1)
- Confidence
- 2
- Informativeness
- 1
- Presentation
- 2
- Soundness
- 2
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Paper summary
This paper investigates the interface sensitivity of LLM agents that use tools, where semantically equivalent modifications to tool names, argument names, tool ordering, or the inclusion of similar tools can markedly harm task performance. The authors argue that standard post-training and multi-interface/domain-randomization methods optimize task performance only independently for each interface, and therefore do not explicitly promote equivalent policies for equivalent interfaces. They propose Cross-Interface Policy Regularization (CIPR), which canonicalizes tool and argument names, builds a paired perturbed interface with known tool correspondences, and regularizes the KL divergence between action distributions over equivalent tools. CIPR consists of a rescoring consistency term, which compares relabeled versions of the same response, and a rollout consistency term, which compares the average action distributions from independently sampled rollouts under the two interfaces. Experiments using GRPO post-training on BFCL with Qwen2.5-3B and Qwen3.5-4B show that CIPR generally improves robustness to held-out interface perturbations while preserving accuracy on the original interface, outperforming multi-interface training by a modest margin. A supervised self-distillation experiment on WebShop further indicates that CIPR can improve robustness to renamed actions.
Critical strengths
1.The paper addresses a real failure mode of tool-using agents: reliance on tool names, positions, and other interface-specific shortcuts. Robustness to changing tool registries and schemas is important for deploying agents in dynamic environments.
2.The distinction between independently scoring multiple interfaces and explicitly regularizing equivalent interfaces is well motivated. Comparing distributions over correspondence-matched actions is more appropriate than directly comparing output tokens when tool names change.
3.The paper evaluates both reinforcement-learning and supervised post-training, uses two different model backbones, tests multiple held-out perturbation types, and includes WebShop, τ²-bench, RoTBench, ablations, and error analysis.
Critical weaknesses
1.The method depends on a strong inference-time canonicalization assumption. CIPR does not make the policy fully robust to arbitrary names by itself. The deployment system must canonicalize every interface before the model sees it. This limits the claim from general interface robustness to robustness under a specific wrapper or adapter architecture, which may not be available in realistic third-party tool ecosystems.
2.Much of the improvement appears to come from canonicalization, training on perturbed interfaces, and especially degraded twins. On BFCL, CIPR improves over multi-interface training by roughly 1 point on Qwen3.5-4B and 1.9 points on Qwen2.5-3B in the aggregate held-out score, with several per-condition differences within the reported confidence intervals.
3.The empirical evidence is not consistently favorable across robustness benchmarks. On RoTBench, CIPR is not uniformly better than multi-interface training and can be substantially worse in the canonical condition for Qwen3.5-4B. This raises questions about whether the proposed regularizer generalizes beyond the specific perturbation family used to construct the training interfaces.
4.The experiments use models up to 9B parameters, mostly single-turn function calling, and one training run per configuration. The rollout consistency term is computationally expensive, but there is no systematic analysis of its cost-performance tradeoff, scaling behavior, or robustness across random seeds and larger multi-turn environments.
Questions for authors
1.How much of the reported gain is attributable specifically to the KL regularization rather than canonicalization, twin expansion, and interface randomization?
2.Can the authors evaluate CIPR without an inference-time canonicalization adapter, or explain how the adapter can be reliably deployed when tools are dynamically registered by external providers? In particular, how should the system handle new tools for which canonical names and argument mappings are not known in advance?
3.What is the computational overhead of the rollout consistency term in realistic training?
2 comments
Thanks for response.
The response solve my most concern, and I will increase the score to 2.
We thank the reviewer for their feedback. In the following, we address their questions and concerns.
On canonicalization and newly registered tools.
The wrapper is a deterministic string mapping that needs no prior knowledge of the tools. For each request, it replaces the names of the available functions and their arguments, so a newly registered
lookup_order(order_id)becomesfunction_01(arg_01)while its description and the argument values stay unchanged, and it translates the model's call back before execution. The provider's API is not modified, and the mapping costs negligible time compared with LLM inference. Correspondences between functions are needed only to construct training samples. Behind the wrapper, CIPR makes the model independent of tool identifiers, tool order and added tools. We keep the original names out because they can still bias the model. When the two WebShop actions are swapped, so that each name suggests the other action, reward falls to zero for both the released and the trained agent (Figure 3).On the contribution of KL versus the training perturbations.
Both the training perturbations and the KL penalties are our contributions. We rename and reorder the functions and add a degraded copy of every function, such as one marked as deprecated, so the presence of a duplicate cannot identify the answer. The multi-interface baseline removes only the KL penalties, so it measures what the KL adds to our other contributions. The complete recipe raises mean accuracy under perturbation over standard post-training by 15.5 and 4.3 points, and by 6.6 and 7.3 points when standard post-training is evaluated with canonical names (Table 1). The intervals in Table 1 are at most $\pm$2.0 points, so any difference between two models above 2.8 points is significant even without pairing. The gain from the KL itself is consistent, as CIPR is more accurate than multi-interface training on 34 of the 38 held-out types across the two backbones (Tables 6 and 7). In Table 2, removing the KL lowers accuracy on explicit cost and latency by 1.9 points and removing the degraded copies by 5.5. Our AgentLM experiments is trained only by self-distillation with the CIPR KL terms and is evaluated with canonical names before and after training, and its WebShop reward rises from 75.7 to 81.0. The gain therefore comes from neither the wrapper nor further supervised fine-tuning.
On whether the gains require duplicating every tool (new experiment).
DR-Full [1] is trained with RL on interfaces randomized over the sixteen static perturbation types introduced in [1], which include the typo, distractor and explicit cost and latency perturbations of Table 1. DR-Full-CIPR adds the CIPR KL terms between the original and the perturbed interface of each DR-Full training sample, instead of our degraded tool interface used in Table 1. Over DR-Full, mean BFCL accuracy under perturbation rises from 57.2% to 69.4% with canonical names for both models, while accuracy on the original interface stays comparable (73.2% and 74.2%), so the drop under perturbation falls from 16.0 to 4.8 points (Table in the common rebuttal response). The largest gain is on the held-out implicit cost and latency perturbations, where accuracy rises from 46.1% to 67.2%. CIPR therefore improves robustness without our multiple interfaces, both on perturbation types seen in training and on a held-out one.
On generalization across robustness benchmarks.
Table 1 already tests generalization beyond the training perturbations, on thirteen perturbation types from RobustBench-TC [1] that are not used in training (Tables 6 and 7 give the results per type). τ2-bench is an out of distribution benchmark that checks that robustness training does not reduce performance, and it does not. Each entry has a standard error of about $\pm$6 to 7 points on airline and $\pm$2 to 6 on retail, and on the original interface no difference between two models of the same backbone is statistically significant. On RoTBench with canonical names (Table 10), accuracy over the corrupted levels rises from 33.7 for standard post-training to 36.3 for CIPR on the 3B model, and from 31.3 to 39.7 on the 4B model.
On model scale, multi-turn tasks and training seeds.
On the multi-turn τ2-bench, robustness training does not reduce performance, as shown above. The per type gains of the KL above hold on two independently trained backbones.
On training overhead.
Compared with multi-interface training, neither KL term requires additional generation. The rollout term compares responses that multi-interface training already generates under the original and the perturbed tool list, and the rescoring term reuses an existing response with the function names changed throughout. The only added cost is computing the probabilities and their gradients on these responses.