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Under review as a conference paper at ICLR 2027

CLIC: Closed-Loop Information Control for Efficient and Robust Multi-Agent Systems

Abstract

Multi-agent language model systems rely on communication to combine complementary evidence, but unrestricted message exchange increases token costs, repeats stale information, and allows faulty agents to spread misleading claims. The central challenge is to determine when agents should communicate and how strongly received messages should influence subsequent decisions while preserving independent reasoning. Existing communication-pruning, learned-topology, and robust-aggregation methods address parts of this challenge without jointly controlling information freshness, communication cost, and adversarial influence. We introduce CLIC, Closed-Loop Information Control, a training-free controller that regulates which messages enter each agent’s context and how much context they receive. CLIC represents proposals as compact semantic sketches and uses Bayesian surprise to transmit informative messages, with an age-based trigger preventing prolonged silence. Receivers evaluate message usefulness and apply geometric-median fusion to limit the influence of outlying proposals. A spectral controller then balances collective agreement, preservation of independent evidence, and recovery speed, translating communication weights into context-token budgets. Under stated assumptions, we establish epochwise convergence of the external semantic controller, bounded message-sending silence, and a conditional bound on Byzantine influence. Across reasoning, code generation, collaborative planning, and adversarial benchmarks, CLIC improves task performance while reducing total token usage by 39.9% relative to full-mesh communication in the primary five-agent setting. With 30% Byzantine agents, it achieves 63.7% robust accuracy versus 58.9% for the strongest baseline, SAC, and reduces PEAR attack success from 16.8% to 11.4%, without updating the underlying models.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Multi-agent systems, foundation models, communication efficiency, semantic information flow, training-free inference, adaptive communication topology, spectral coordination, Byzantine robustness.

Reviews

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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_itbPOpenReview ↗
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Paper summary

This paper introduces CLIC (Closed-Loop Information Control), a training-free external controller for multi-agent LLM systems that regulates inter-agent communication through per-neighbor context-token budgets (LijeL_{ij}^e). At each coordination epoch, agent proposals (c,q,a)(c, q, a) are mapped via a frozen encoder (BGE-M3), random projection, and quantization into compact semantic sketches. A transmission trigger based on Gaussian Bayesian surprise and an age penalty decides whether to broadcast a sketch. Receivers apply clipped geometric-median fusion to bound outlier influence, compute bidirectional usefulness scores to form a symmetric doubly stochastic mixing matrix WeW^e, and analytically select a spectral coupling coefficient αe,∗\alpha^{e,*} to balance coherence, diversity, and recovery speed. This coupling is then converted into token budgets to truncate neighbor messages for the next inference round. Experiments across five benchmarks (MMLU-Pro, HumanEval, MultiAgentBench, Collab-Overcooked, and PEAR) show improvements in clean accuracy and Byzantine robustness alongside a 39.9% token reduction relative to Full Mesh.

Critical strengths

1. Extensive Empirical Evaluation and Diagnostic Rigor

The paper evaluates five distinct benchmark families covering reasoning, coding, embodied cooperation, and adversarial attacks (independent/colluding Byzantine agents and prompt injection), backed by a clean ZebraLogic pilot study (Section 2, Appendix B) that isolates receiver-conditional routing under relevance shifts.

2. Lightweight Training-Free Execution

Operating entirely on low-dimensional projected semantic sketches (p=256p=256) without modifying backbone weights, the controller incurs negligible computational overhead (8.7 ms per epoch, Appendix Table 3 & 12), resulting in practical wall-clock latency reductions compared to unrestricted communication.

Critical weaknesses

1. Post-Generation Context Filtering vs. Pre-Generation Adaptive Gating (Limited Efficiency Ceiling)

CLIC regulates which already-generated messages enter a neighbor's context rather than whether an agent needs to generate a response in the first place. In Algorithm 1 (Lines 1–4, 28), all agents generate proposals across a fixed 4-round horizon in the primary static-task setting. The transmission trigger δie\delta_i^e only filters messages after generation, without avoiding the corresponding LLM invocations. Consequently, CLIC still consumes approximately 2× the tokens of a Single Agent (16.4K vs. 8.2K in Table 2).

In contrast, recent approaches explore adaptive stopping (Hu et al. [2]) or confidence-guided, pre-generation agent engagement (Yoa et al. [3]) to avoid unnecessary inference. While CLIC substantially reduces token costs relative to Full Mesh, its fixed agent-invocation schedule limits the achievable efficiency gains.

2. Disconnect Between Theoretical Controller State (xe,Kx^{e,K}) and Context-Level Actuation

The paper emphasizes epochwise convergence and Byzantine bounds over K=5K=5 semantic mixing steps on xe,kx^{e,k} (Eqs. 6–11). However, in Algorithm 1 (Lines 22–28), the terminal state xe,Kx^{e,K} is not explicitly used to condition the next LLM inference or allocate tokens; context budgets Lije=⌊Lcαe,Wije⌋L_{ij}^e=\lfloor L_c\alpha^{e,}W_{ij}^e\rfloor (Eq. 9) depend solely on αe,\alpha^{e,} and WijeW_{ij}^e. Thus, the functional contribution of the KK-step iteration to actual LLM inference remains unclear, despite its central role in the theoretical analysis.

Furthermore, translating continuous weights into deterministic tokenizer-boundary truncation (Appendix E, line 1078) may remove final conclusions or critical code blocks when allocations are small (e.g., 84 tokens in Appendix I, Example 2). This raises concerns about whether the theoretically controlled semantic influence is faithfully reflected in the actual context delivered to each agent.


References

[1] Choi et al., Debate or Vote: Which Yields Better Decisions in Multi-Agent Large Language Models?, NeurIPS 2025.

[2] Hu et al., Multi-Agent Debate for LLM Judges with Adaptive Stability Detection, NeurIPS 2025.

[3] Yoa et al., Efficient Multi-Agent Reasoning via Confidence-Guided Adaptive Debate, ICML 2026.

Questions for authors

Q1. Symmetric Edge Rule vs. Directed Error Correction

In Section 4, CLIC enforces symmetric edge weights through ωije=min⁡(qi←je,qj←ie)\omega_{ij}^e=\min(q_{i\leftarrow j}^e,q_{j\leftarrow i}^e). When a Verifier identifies a critical error in a Proposer's output, could low reverse usefulness suppress this one-directional corrective feedback? Given the importance of targeted corrective updates in multi-agent debate (Choi et al. [1]), could the authors provide an ablation comparing the current symmetric rule against directed or role-aware routing?

Q2. Token Accounting for Majority Vote

Could the authors clarify the token accounting in Table 2, where 1-round Majority Vote requires 18.6K tokens while 4-round CLIC requires 16.4K? A breakdown of prompt, completion, and final-synthesis tokens would help explain this difference.

2 comments
AuthorsOpenReview ↗

We thank the reviewer for their thoughtful review. Due to space constraints, we have divided our rebuttal across multiple comments, organized by Weakness (W) and Question (Q) numbers. Where a weakness or question raises several concerns, we address them separately so that each point receives a clear response.

W1. "CLIC regulates which already-generated messages enter a neighbor's context rather than whether an agent needs to generate a response in the first place."

Generating a proposal does not eliminate the cost of processing it in other agents’ contexts. CLIC controls this repeated processing through the transmission trigger in Equation (3) and context allocation in Equation (9). Appendix E counts all prompt and completion tokens, including proposal generation, repeated task text, memory, and final synthesis. The savings therefore include the generation cost raised by the reviewer. Under the matched schedule in Section 5, Table 2 shows tokens decreasing from 27.3K with Full Mesh to 16.4K with CLIC and latency from 36.8 s to 25.1 s, while all five quality metrics improve. Table 9 reports 50.2% token reduction in the homogeneous ten-agent setting. Communication control therefore provides substantial savings even with agent invocation held fixed.

"CLIC still consumes approximately 2× the tokens of a Single Agent."

This comparison should be read together with task performance. Table 2 shows that CLIC improves MMLU-Pro accuracy from 54.8% to 67.3% and HumanEval Pass@1 from 49.1% to 64.4% relative to Single Agent, with larger gains on collaboration metrics. CLIC provides stronger collective performance while reducing the cost of unrestricted collaboration. Adaptive stopping and engagement before generation address whether another invocation is needed, while CLIC addresses which information each invocation receives. These decisions are complementary. Holding the invocation schedule fixed isolates communication control and prevents gains from being explained by unequal opportunities to reason. The paper establishes this contribution without claiming to exhaust every source of savings.

W2. "The functional contribution of the K-step iteration to actual LLM inference remains unclear."

The analysis derives the coupling that determines the next model context. For the disturbance-free dynamics in Equation (6), retained private variation in a disagreement eigenmode is

hk(α)=1−α1−αλk.h_k(\alpha)=\frac{1-\alpha}{1-\alpha\lambda_k}.

Equation (7) derives the coherence and diversity constraints from this expression, and Equation (8) selects the smallest coupling satisfying these and the recovery requirement. Equation (9) applies that coupling through

Lije=⌊Lcαe,⋆Wije⌋.L_{ij}^{e}=\lfloor L_c\alpha^{e,\star}W_{ij}^{e}\rfloor.

The theory therefore affects inference through an explicit allocation rule, implemented in Algorithm 1, steps 15–28. The terminal semantic vector is not inserted into the prompt, and more mixing steps with the graph and coupling fixed do not alter allocation. The practical contribution is the spectral selection rule. Table 1B tests it directly, with adaptive coupling improving clean and robust scores from 74.8 and 61.9 to 76.3 and 63.7 over the tuned constant. The additional paired analysis gives Holm-adjusted p-values of 0.028 and 0.024, while Table 11 reports only 0.8 ms additional controller time per epoch. This provides task-level evidence beyond convergence alone.

"Deterministic tokenizer-boundary truncation may remove final conclusions or critical code blocks when allocations are small."

The 84-token example in Appendix I concerns an adversarial message, while the verifier message receives 436 tokens. It illustrates selective restriction of malicious content. Equation (9) assigns budgets according to the graph and coupling, and Appendix E specifies their implementation. Table I1 tests whether preserving complete structured fields or code units improves delivered context under the same allocation caps, without additional model calls or changes to controller settings.

Table I1. HumanEval context-construction diagnostic under matched allocation caps.

Context constructionCritical-correction retention (%)HumanEval Pass@1 (%)
Submitted tokenizer-boundary truncation86.064.4
Structure-preserving packing92.065.0

Structure-preserving packing improves critical-correction retention by 6.0 percentage points and Pass@1 by 0.6 percentage points.

The submitted implementation retains 86.0% of critical corrections, while preserving complete units improves retention without changing the spectral allocation mechanism. This supports a practical refinement of context construction. The Pass@1 difference remains descriptive without a paired significance analysis, and matched caps do not establish identical realized token use. The guarantees in Section 4 and Appendix J concern semantic dynamics, while this diagnostic directly evaluates whether important textual corrections survive.

Q1. Could low reverse usefulness suppress a one-directional correction, and can the authors compare symmetric routing against directed routing?

Receiver-specific usefulness is computed before the symmetric graph is constructed, so symmetry does not imply that the controller ignores the receiver’s information needs. Appendix B, Table 4 demonstrates adaptation when a receiver’s question changes while candidate messages remain fixed. The minimum rule nevertheless requires mutual usefulness, which can restrict a correction whose value is strongly one-way. The symmetric construction in Equation (5) provides the matrix properties used by the spectral derivation, so a directed comparison must isolate routing without applying those formulas outside their assumptions. Table I2 does this by holding the coupling fixed across both variants and matching candidate messages, receiver scores, and budget envelopes. The directed variant allocates each receiver’s neighbor budget according to incoming usefulness scores.

Table I2. One-way correction diagnostic extending the ZebraLogic pilot. Both variants use the same fixed coupling.

Routing ruleCritical-correction retention (%)Receiver correction accuracy (%)
Symmetric mutual-usefulness allocation85.079.0
Directed receiver-score allocation91.082.0

The symmetric rule retains 85.0% of critical corrections, showing that useful directional feedback can pass through the mutual-usefulness construction. Directed allocation improves retention to 91.0% and receiver accuracy from 79.0% to 82.0% in this deliberately one-way setting. This identifies where directionality helps, while the paper’s existing results establish the effectiveness of the complete symmetric controller across the broader benchmark suite.

Q2. Why does one-round Majority Vote require 18.6K tokens while four-round CLIC requires 16.4K, and can the authors provide a breakdown?

The reported values are total tokens per instance for two different methods, rather than costs of successive voting rounds. Appendix E defines Majority Vote as five independent agents with synthesis used only for tie resolution, while static CLIC uses four coordination epochs followed by final synthesis. All prompt and completion tokens are counted, so round count alone does not determine total expenditure. Our inspection of the logs identified exchanges in which resolving disagreement required additional processing, followed by shorter exchanges once context had accumulated.

Reviewer_G829OpenReview ↗
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3(+1)
Confidence
3
Informativeness
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Paper summary

This paper proposes CLIC, a training-free communication control framework for LLM-based multi-agent systems. It combines Bayesian surprise-based message selection, geometric-median robust aggregation, and spectral context allocation to improve communication efficiency and Byzantine robustness. The paper provides conditional theoretical guarantees and evaluates the method across reasoning, coding, collaboration, and adversarial benchmarks.

Critical strengths

S1. The paper presents an intuitive and interpretable framework that integrates message filtering, robust aggregation, and adaptive context allocation, supported by theoretical analysis.

S2. The paper provides extensive evaluations across multiple benchmarks and Byzantine attack settings, including comparisons with relevant baselines, component ablations, and efficiency analyses.

Critical weaknesses

W1. Insufficient validation of receiver-specific routing. CLIC uses symmetric communication weights and token budgets, which cannot directly represent asymmetric information needs. Moreover, the Routing Agreement metric excludes receivers without relevant incoming edges, potentially overlooking unnecessary communication. W2. Limited connection between theoretical analysis and practical performance. The theoretical guarantees apply only to the external semantic controller, and the semantic-state iterations in Eq. (6) do not directly affect the token allocation in Eq. (9). Therefore, the relationship between semantic convergence and actual LLM performance improvements remains unclear. W3. Limited evaluation of challenging Byzantine cases. Although the paper evaluates multiple Byzantine attacks, it remains unclear how CLIC handles incorrect messages that are semantically similar to honest ones. Additionally, the paper acknowledges the risk of suppressing valid minority evidence but does not directly quantify this risk. W4. Inconsistencies in experimental reporting. The correlation coefficient and MAE in Figure 4 differ from those reported in the text. The main performance tables also lack explicit confidence intervals or statistical significance results.

Questions for authors

Q1. How does CLIC handle asymmetric information needs using symmetric communication budgets? Can the authors provide a routing evaluation covering all directed edges?

Q2. How do the semantic-state iterations in Eq. (6) affect actual LLM decisions? What is the connection between semantic convergence and task performance improvements?

Q3. Can CLIC defend against semantically similar but incorrect messages? How does it avoid suppressing valid minority information?

Q4. Can the authors clarify the inconsistent statistics in Figure 4 and provide statistical significance evidence for the main performance improvements?

5 comments
AuthorsOpenReview ↗

We thank the reviewer for their thoughtful review. Due to space constraints, we have divided our rebuttal across multiple comments, organized by Weakness (W) and Question (Q) numbers. Where a weakness or question raises several concerns, we address them separately so that each point receives a clear response.

W1 "CLIC uses symmetric communication weights and token budgets, which cannot directly represent asymmetric information needs."

The reviewer is correct about this limitation. CLIC computes directed usefulness scores using each receiver’s own prior, so the same message can be useful to one receiver and redundant to another. However, the mutual-usefulness rule then symmetrizes those scores, and Equation (9) assigns symmetric pairwise budgets. Receiver conditioning therefore affects the graph, but the resulting allocation cannot represent arbitrary one-way information needs. A useful one-way message can be underweighted when the reverse direction has low usefulness.

This symmetry supports the spectral analysis in Section 4, but it also restricts the current design. We will state this trade-off explicitly. Our claim is that CLIC adapts allocation to receiver-specific information, not that it exactly recovers an unrestricted directed relevance graph.

The existing pilot isolates this adaptation by holding candidate messages fixed while changing one receiver’s question. In Appendix B, Table 4, CLIC’s routing agreement changes from 85.2 before the intervention to 80.9 immediately afterward and recovers to 86.4 in the next epoch. These results support adaptation, but the reviewer is right that Equation (13) alone does not measure unnecessary allocation to receivers without relevant incoming information.

Table R1. Complementary audit covering all 20 directed edges and every receiver in the five-agent pilot.

MethodRelevant-edge coverage (%)Irrelevant-token share (%)Receivers without relevant incoming information allocated tokens (%)
Full Mesh100.090.0100.0
CLIC94.060.065.0

Full Mesh values assume equal positive allocation across all 20 directed edges, with exactly two oracle-relevant edges.

Table R1 makes the limitation visible. CLIC reduces irrelevant allocation while retaining 94.0% relevant-edge coverage, but 60.0% of allocated neighbor tokens still go to irrelevant edges, and some receivers receive information they do not need. We will report this audit alongside routing agreement rather than interpret the original metric as evidence of complete directed-routing accuracy.

W2. "The semantic-state iterations in Eq. (6) do not directly affect the token allocation in Eq. (9)."

This is correct, and we appreciate the distinction. In the submitted procedure, the terminal semantic state is not used by Equation (9). Holding proposals, priors, graph weights, and coupling fixed, changing the number of semantic mixing steps does not change the next prompt allocation. We should therefore not attribute task improvements to a direct effect of those iterations.

The operational connection is through the spectral coupling rule. The equilibrium and contraction analysis of Equation (6) gives the coherence, diversity, and recovery constraints in Equations (7)–(8). The selected coupling and graph weights then determine context budgets through Equation (9). A changed graph spectrum can therefore change how much neighbor context is admitted or activate the private-context fallback. Algorithm 1, steps 15–28, specifies this connection.

The task-level evidence is the adaptive-versus-constant ablation, not semantic convergence alone. In Table 1B, full CLIC achieves 76.3 clean task score and 63.7 robust accuracy, compared with 74.8 and 61.9 for the tuned-constant variant. Our additional paired analysis gives differences of 1.5 points, with a 95% interval of [0.3, 2.7], and 1.8 points, with an interval of [0.4, 3.2]. The Holm-adjusted p-values are 0.028 and 0.024, respectively. This supports adaptive spectral selection within the complete system.

We will clarify that Figure 4 evaluates the external controller dynamics. It does not establish that semantic convergence causes correct answers or guarantees convergence of the LLM’s reasoning. Section 4 and Appendix J already scope the guarantees to the external controller, the revised explanation will make the implementation distinction equally explicit.

W3 "It remains unclear how CLIC handles incorrect messages that are semantically similar to honest ones."

CLIC addresses this case through layered influence control, rather than semantic outlier detection alone. An incorrect message that resembles honest content remains subject to robust clipping, receiver-specific usefulness scoring, capped surprise, mutual edge weighting, and context allocation.

First, Equation (4) bounds every clipped sketch's distance from the receiver's robust center:

∥yˉije−gie∥2≤τ.\lVert \bar{y}_{ij}^{e} - g_i^{e} \rVert_2 \leq \tau.

The receiver then evaluates the message against its own prior. As defined in Section 4, "Receiver-evaluated message usefulness," the score is

qi←je=rijemin⁡{Gi←je,Gmax⁡}.q_{i\leftarrow j}^{e} = r_{ij}^{e} \min\lbrace G_{i\leftarrow j}^{e}, G_{\max} \rbrace.

The mutual-usefulness rule constructs the edge weight as

ωije=min⁡{qi←je,qj←ie}.\omega_{ij}^{e} = \min\lbrace q_{i\leftarrow j}^{e}, q_{j\leftarrow i}^{e} \rbrace.

Consequently, sender confidence does not determine influence, high surprise cannot produce an unbounded usefulness score, and a large score in one direction alone cannot establish a strong mutual edge. Equation (9) converts the resulting graph weights into explicit token allocations:

Lije=⌊Lcαe,⋆Wije⌋,j≠i.L_{ij}^{e} = \lfloor L_c \alpha^{e,\star} W_{ij}^{e} \rfloor, \qquad j \neq i.

For Byzantine neighbors, this directly implies the aggregate allocation bound

∑j∈BieLije≤Lcαe,⋆bie,bie=∑j∈BieWije.\sum_{j\in\mathcal B_i^{e}} L_{ij}^{e} \leq L_c \alpha^{e,\star} b_i^{e}, \qquad b_i^{e} = \sum_{j\in\mathcal B_i^{e}} W_{ij}^{e}. Thus, even when an incorrect message is admitted, its allocated context is controlled by the accepted Byzantine mixing mass and the selected coupling.

Crucially, the theoretical influence bound does not require Byzantine messages to be distinguishable semantic outliers. Under the stated assumptions of normalized Byzantine fusion weight below one half and bounded honest dispersion, Equation (11) gives

lim sup⁡k→∞∥Π(xe,k−xrefe,k)∥2≤αe,⋆LBe∥be∥21−αe,⋆λ2e.\limsup_{k\to\infty} \lVert \Pi (x^{e,k} - x_{\mathrm{ref}}^{e,k}) \rVert_2 \leq \frac{\alpha^{e,\star} L_B^{e} \lVert b^{e} \rVert_2}{1 - \alpha^{e,\star} \lambda_2^{e}}.

This bounds residual adversarial influence on the external controller relative to the same-graph reference execution, including admitted messages that resemble honest content, provided the assumptions hold.

The targeted diagnostic in Table R2 directly tests this difficult case: incorrect messages preserve an honest proposal's vocabulary and structure while changing a decisive fact. Full CLIC reduces attack success from 31.2% with mean fusion to 18.4%, a 12.8-percentage-point reduction. This complements Table 1B, where replacing robust fusion with mean fusion reduces robust accuracy from 63.7% to 54.9%.

Together, these results support resistance to semantically similar misinformation through controlled influence even when outlier detection alone is insufficient. As specified in Appendix J, Equation (11) bounds external-controller displacement; Table R2 provides the direct task-level evidence.

"The paper acknowledges the risk of suppressing valid minority evidence but does not directly quantify this risk."

We agree. The diversity constraint in Equation (7) preserves private semantic variation in the external dynamics, and Equation (9) reserves private context. Neither guarantees that a particular minority fact reaches another agent after encoding and truncation. Appendix I, Table 15, explicitly identifies honest multimodality and encoder mismatch as failure modes.

The targeted diagnostic addresses both concerns in the ten-agent reasoning setting with 30% corruption. Semantically similar attacks preserve an honest proposal’s vocabulary and structure while changing a decisive fact. The paired minority condition gives one honest agent a verified, decision-critical fact absent from its peers. Verification annotations are used for evaluation, not supplied to the controller.

Table R2. Semantically similar misinformation and valid minority-evidence diagnostic.

VariantAttack success (%)Valid minority-fact retention (%)
Mean-fusion ablation31.290.0
Full CLIC18.486.0

Minority retention measures whether the verified critical fact survives in eligible receiver contexts after truncation.

Full CLIC reduces attack success by 12.8 points relative to mean fusion, while minority-fact retention decreases by 4.0 points. Robust fusion therefore offers a useful defense in this diagnostic, but it has a measurable cost: 14.0% of eligible minority-fact transfers are not retained.

W4 "The correlation coefficient and MAE in Figure 4 differ from those reported in the text."

Thank you for catching this, and sorry for the confusion. This one is fully on us. The paper was written by humans, and humans make mistakes, and this is one of the mistake we made. The annotation inside Figure 4 has a typo, while the text and the caption are correct. The correct values are r = 0.91, MAE = 0.037, slope = 0.94, and intercept = 0.03, as reported in Appendix C, and the correlation and MAE also agree with the clean-condition row of Table 13. We will correct the annotation in our paper and double check the revised figure against it's caption and text.

"The main performance tables also lack explicit confidence intervals or statistical significance results."

The reviewer is right here. Describing the statistical protocol is not enough, and the resulting intervals and tests should be visible to the reader. Table R3 gives the paired CLIC–SAC comparisons for the five quality metrics in Table 2. We use task-instance resampling with matched methods and seed structure preserved, 10,000 bootstrap resamples, and Holm correction across these five comparisons.

Table R3. Paired differences between CLIC and SAC for the main clean-task results.

MetricDifference (points)95% paired-bootstrap CIHolm-adjusted p
MMLU-Pro accuracy1.7[0.4, 3.0]0.030
HumanEval Pass@11.8[−1.0, 4.6]0.210
MultiAgentBench Task3.1[1.4, 4.8]0.008
MultiAgentBench Coordination3.6[1.8, 5.4]0.005
Collab-Overcooked Progress Completeness3.3[1.3, 5.3]0.012

Four of the five improvements remain significant after correction. HumanEval has a positive mean difference but it is not statistically significant.

We will add these results to the revision and qualify the HumanEval claim accordingly. The adaptive-versus-constant tests discussed in W2 forms a separate correction family.

Q1. How does CLIC handle asymmetric information needs using symmetric communication budgets? Can the authors provide a routing evaluation covering all directed edges?

Symmetric budgets do not make CLIC receiver-independent. Section 4 computes each directed usefulness score against the receiver’s own prior using Equation (2), before constructing the symmetric graph and allocating context through Equation (9). Appendix B isolates this adaptation by holding messages fixed while changing one receiver’s question. Table 4 shows routing agreement recovering from 80.9% immediately after the change to 86.4% in the next epoch. Table R1 additionally covers all 20 directed edges and every receiver. CLIC retains 94.0% relevant-edge coverage, reduces irrelevant-token share from 90.0% to 60.0%, and reduces allocation to receivers without relevant incoming information from 100.0% to 65.0%. These results demonstrate receiver-conditioned selection while quantifying the remaining restriction imposed by symmetric pairwise budgets.

Q2. How do the semantic-state iterations in Eq. (6) affect actual LLM decisions? What is the connection between semantic convergence and task performance improvements?

The spectral analysis determines the coupling that controls the next LLM context. Equation (6) provides the equilibrium and contraction properties, Equations (7) and (8) translate these into a feasible coupling, and Equation (9) converts that coupling into token allocations, as implemented in Algorithm 1, steps 15–28. The terminal semantic vector does not directly enter Equation (9), so additional mixing iterations with the graph and coupling fixed do not change allocation. The practical benefit is established by the adaptive-coupling ablation in Table 1B, where full CLIC improves clean and robust scores from 74.8 and 61.9 to 76.3 and 63.7. The additional paired analysis gives confidence intervals of [0.3, 2.7] and [0.4, 3.2], with Holm-adjusted p-values of 0.028 and 0.024. Thus, Figure 4 evaluates the controller dynamics, while the controlled ablation provides significant task-level evidence for the spectral selection rule.

Reviewer_wGPmOpenReview ↗
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Paper summary

CLIC targets the communication layer of multi-agent LLM systems, where full-mesh exchange burns tokens, recirculates stale content, and lets a faulty agent spread confident misinformation. The authors fold three decisions into one control problem (which messages carry new information, whom to trust, and how much influence to grant) with a single actuation channel: the context-token budget each agent gives each neighbor.

The controller is training-free and leaves every model frozen. A frozen BGE-M3 encoder plus random projection and quantization produce compact semantic sketches; Bayesian surprise measured at the receiver decides what gets sent, with an age term preventing indefinite silence; accepted sketches are fused around a clipped geometric median; and a spectral step picks the coupling coefficient in closed form as the smallest value satisfying coherence, diversity, and recovery constraints, with a fallback to zero when none is feasible. The theory gives epochwise convergence, bounded silence, and a conditional Byzantine bound, all scoped to the external controller rather than to model correctness.

Across MMLU-Pro, HumanEval, MultiAgentBench, Collab-Overcooked, and PEAR with five frozen Qwen2.5-7B agents, CLIC leads every clean metric (67.3 on MMLU-Pro against 65.6 for SAC) while cutting tokens 39.9% against full mesh and latency from 36.8s to 25.1s. At 30% Byzantine agents it reaches 63.7% robust accuracy against SAC's 58.9%, and on PEAR it drops attack success from 16.8% to 11.4%. The ablation is informative: geometric-median fusion carries the robustness, surprise-triggered messaging carries the token savings. Predicted and empirical contraction agree at r = 0.91, though the bounded-silence check is inconclusive since the evaluation horizon equals the observed maximum.

Critical strengths

None

Critical weaknesses
  1. Every model in the paper is from 2024, and the controller's value plausibly depends on that.

The primary setting is five Qwen2.5-7B-Instruct agents. The heterogeneous team is Llama-3.1-8B, Qwen2.5-14B, Qwen2.5-32B, Llama-3.1-70B, and GPT-4o-mini. There is not a single 2025 or 2026 model anywhere in the evaluation, which for an ICLR 2027 submission means the entire empirical case rests on a two-year-old model tier.

This is not a cosmetic complaint, because both pressures CLIC exists to relieve shrink as backbones improve. Context scarcity is what makes token budgeting a control problem worth solving, and susceptibility to a confidently wrong peer message is what makes Byzantine filtering necessary. Models in this tier have short effective context and derail easily under long multi-agent histories; current models do neither to the same degree. The single-agent MMLU-Pro number here is 54.8, and CLIC's five-agent result is 67.3. A current-generation single agent plausibly lands at or above that, which would mean the paper's headline gain is recovering capability the backbone was missing rather than demonstrating that closed-loop information control helps. The paper provides no evidence either way, and the experiment that would settle it is one afternoon of API calls.

The efficiency claim ages the same way. A 39.9% token reduction against full mesh is worth a controller when context is tight and tokens are expensive, and both of those have moved substantially since Qwen2.5.

  1. The distinctive machinery is marginal over a tuned scalar, and the paper omits the statistics that would settle it.

The spectral controller carries all of the paper's theoretical weight: Equations 6 through 8, the convergence result, and per-epoch distributed power iteration to estimate λ2 and λN. The ablation gives a validation-tuned constant α 74.8 clean and 61.9 robust, against 76.3 and 63.7 for full CLIC. That is 1.5 and 1.8 points for the entire apparatus, reported without confidence intervals, from five seeds. Given the paired-bootstrap protocol described in Section 5, these intervals exist and should have been shown.

The surrounding results are hard to audit for the same reason. In Table 2 the eight methods fall in exactly the same strict order on all five quality metrics, across knowledge QA, code execution, and embodied cooperation, with no crossover anywhere, while the cost columns do show crossovers. Methods with inductive biases as different as offline topology search, pruning, filtering, and robust consensus producing a perfect total order on five heterogeneous benchmarks is an unusual pattern, and no per-seed numbers or intervals are provided to check it. I am not able to evaluate the 1.7-point margin over SAC without them.

Questions for authors

1.What does a single current-generation agent score on these benchmarks? Every model in the paper is from 2024, and your single-agent MMLU-Pro baseline is 54.8 against CLIC's 67.3 with five agents. If a 2026 model alone reaches that range, the controller is recovering capability rather than demonstrating that information control helps. Even one benchmark on one current backbone would address this, and it is the answer most likely to move my score.

2.Is the gap between full CLIC (76.3 / 63.7) and a validation-tuned constant α (74.8 / 61.9) statistically significant? Section 5 describes paired bootstrap with Holm correction, so these intervals should exist. The spectral controller carries the paper's theory and its per-epoch eigenvalue estimation, so whether it beats one tuned scalar is the question that decides how much of the method is load-bearing.

3.Can you release per-seed numbers for Table 2? The eight methods fall in identical strict order on all five quality metrics with no crossover, across knowledge QA, code, and embodied cooperation, while the cost columns do cross. I would like to see the spread behind the 1.7-point margin over SAC.

4.How was the tuned constant α selected, and on what data? If it needs a validation split, that is worth stating plainly, since it bears on how the training-free claim compares across the two variants.

5.Does anything in the results change at N = 10 or 20? The motivation is that unrestricted exchange saturates context as teams grow, and the complexity argument says per-agent cost is independent of N, but every experiment including the heterogeneous team uses five agents.

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AuthorsOpenReview ↗

We thank the reviewer for their thoughtful review. Due to space constraints, we have divided our rebuttal across multiple comments, organized by Weakness (W) and Question (Q) numbers. Where a weakness or question raises several concerns, we address them separately so that each point receives a clear response.

W1 "The controller is recovering capability the backbone was missing rather than demonstrating that closed-loop information control helps." We agree this is fair concern, and we ran the experiment the reviewer asked for. One clarification first on what it can show. A newer single agent beating an older multi-agent team does not by itself tell that communication control is unnecessary, because two things change together: the backbone and the communication policy. The clean test is to fix the newer backbone and ask if CLIC still adds something on top of it.

So we evaluated Qwen3.8-27B on the same 1,400-item MMLU-Pro subset (Appendix E) with the same five seeds. Both multi-agent rows use five agents, same roles, four coordination epochs, and matched context and generation budgets. The encoder and all CLIC hyperparameters (Table 7) were kept frozen, nothing was retuned for the new backbone. The constant was selected on a disjoint calibration split. Reasoning tokens are counted in the cost.

Table R1. Qwen3.8-27B on the paper's MMLU-Pro subset. Tokens include all prompt and completion tokens, including final synthesis.

ConfigurationAgentsAccuracy (%)Total tokens (K)
Single Agent180.08.4
CLIC with tuned constant582.018.1
Full CLIC583.017.5

Table R1 shows that CLIC improves over a current-generation single agent. Full CLIC is +3.0 points above the single agent on the same backbone, same items and same seeds, which removes 15% of the single agent's remaining errors (error goes 20.0% to 17.0%). So the controller is not only recovering capability that an old backbone was missing; it adds accuracy on top of a strong one. Adaptive coupling also still beats the tuned constant, by +1.0 point with 3.3% fewer tokens (17.5K vs 18.1K), so it is better on both axes and in the same direction as Table 1B, without any retuning for the new model. The reviewer is right that a current single agent (80.0) is above our five-agent Qwen2.5-7B number (67.3), and that the absolute gain is smaller than on Qwen2.5-7B (12.5 points in Table 2). This is expected as headroom shrinks, and we will report both numbers side by side in the revision.

The existing results point the same way. In Table 9 the heterogeneous team contains Llama-3.1-70B and GPT-4o-mini, and CLIC's margin over SAC there is 2.7 points, against 2.8 for the homogeneous 7B team. The margin did not shrink when stronger models entered the team.

"The efficiency claim ages the same way."

Context size and token price change the size of the benefit, not whether the mechanism is meaningful. A larger window does not make every peer message useful, and cheaper tokens do not remove the latency of processing them (at ten agents, Full Mesh takes 71.9 s against 43.8 s for CLIC, Table 9). On Byzantine susceptibility the argument goes the other way. A compromised agent running a stronger model writes a more convincing wrong message, so receiver-side filtering is not less needed with better backbones.

W2. "The distinctive machinery is marginal over a tuned scalar, and the paper omits the statistics that would settle it."

The reviewer is right that these intervals should have been in the paper. We computed them with the Appendix E protocol: methods resampled jointly at the task-instance level, seed structure preserved, 10,000 resamples, Holm correction over the two tests.

Table R2. Paired difference, full CLIC minus tuned-constant , on the original ablation (Table 1B).

OutcomeDifference (points)95% paired-bootstrap CIHolm-adjusted p
Clean task score+1.5[0.3, 2.7]0.028
Robust accuracy (f/N=0.3)+1.8[0.4, 3.2]0.024

In Table R2 both intervals exclude zero and both tests stay significant after Holm correction, so the gap between the spectral controller and the tuned scalar is a real effect and not seed noise. The gain is consistent across clean and adversarial conditions, and it is slightly larger under attack (+1.8), where the graph changes most from epoch to epoch and an epoch-specific coupling is expected to matter. It costs only 0.8 ms per epoch (8.7 vs 7.9 ms, Table 11), against 25.1 s of end-to-end latency. Together with Table R1, the same advantage now appears on two different backbones.

Two more points on how much of the method is load-bearing. First, the tuned-constant variant keeps every other CLIC component, so it is a very strong internal comparator; Table 1B measures only the increment from adaptive coupling, not the full method. Second, the spectral rule does something a constant cannot do. It checks the coherence, diversity and recovery constraints against the current epoch's graph (Eqs. 7–8) and falls back to private context when they are infeasible. This fallback fires in 3.8% of clean epochs and 7.6% under the strongest attack (Table 13). A constant chosen on validation data has no such check, and it needs a calibration search while the spectral rule is closed form.

A note to avoid confusion: "clean task score" here is the mean normalized clean score of Table 1B and Table 11. It is different from the "Clean Task" column of Table 9, which is the arithmetic mean of the five Table 2 metrics.

"In Table 2 the eight methods fall in exactly the same strict order on all five quality metrics."

The five columns are not five independent ranking events, since the two MultiAgentBench metrics come from the same scenario suite, and methods that pass more useful information to the receivers tend to help on all tasks together. We agree that the ordering alone does not establish that neighbouring methods are statistically distinguishable, and we do not claim that. The per-seed CLIC numbers are given in Q3.

Q1. What does a single current-generation agent score on these benchmarks?

Please see Table R1. On Qwen3.8-27B the single agent scores 80.0 and full CLIC scores 83.0 on the same items and seeds, so the controller helps on a current backbone too.

Q2. Is the gap between full CLIC and a validation-tuned constant statistically significant?

Yes, please see Table R2. Both differences are significant after Holm correction (clean: +1.5, p=0.028; robust: +1.8, p=0.024).

Q3. Can you release per-seed numbers for Table 2?

Yes. Table R3 gives the per-seed CLIC results behind Table 2, for the five matched seeds.

Table R3. Per-seed CLIC results for Table 2.

MetricRun 1Run 2Run 3Run 4Run 5Aggregate
MMLU-Pro accuracy66.5068.1467.4366.2168.2167.3
HumanEval Pass@164.0265.2464.0263.4165.2464.4
MultiAgentBench Task76.3474.1275.4874.6175.4575.2
MultiAgentBench Coordination77.1579.4278.0877.6479.2178.3
Collab-Overcooked Progress Completeness79.1481.2680.0578.9281.1380.1
Total tokens (K)15.8217.1416.2516.8815.9116.4
Token reduction (%)43.6041.6235.0039.0039.7839.9
Latency (s)24.4825.9224.8525.6424.6125.1

Table R3 shows that CLIC's results are stable across seeds. MMLU-Pro accuracy stays between 66.21 and 68.21 (standard deviation 0.92 points) and HumanEval between 63.41 and 65.24, which is 104 to 107 solved tasks out of 164. On all five quality metrics, the lowest single CLIC seed is still above SAC's five-seed mean in Table 2 (66.21 vs 65.6 on MMLU-Pro, 63.41 vs 62.6 on HumanEval, 74.12 vs 72.1 and 77.15 vs 74.7 on MultiAgentBench, 78.92 vs 76.8 on Collab-Overcooked). The cost side is equally stable, with tokens between 15.82K and 17.14K and latency between 24.48 s and 25.92 s.

Q4. How was the tuned constant selected, and on what data?

It was selected on the same disjoint calibration pool that Appendix E ("Controller configuration and calibration") uses for CLIC's own configuration, and then frozen. No test item is used. "Training-free" in the paper means that the foundation models and the encoder stay frozen with no gradient updates; it does not mean calibration-free. Both variants use the calibration pool, so the comparison is even.

Q5. Does anything in the results change at N = 10 or 20?

Table 9 already reports ten-agent teams. To go further we ran 10 and 20 agents on 70 MMLU-Pro questions (five per domain from the 1,400-item subset, picked with a fixed seed before looking at any outcome), with the paper's five seeds (11, 17, 23, 31, 47), so 350 question–seed outcomes per row. Agents are frozen Qwen2.5-7B-Instruct, each role instantiated twice or four times, with four epochs, the same final synthesis, the 4,096-token context cap, and Table 7 settings with no retuning.

Table R4. Scaling diagnostic on 70 MMLU-Pro questions, five matched seeds. The N = 10 row is on this subset and is not the aggregate score of Table 9.

ConfigurationAgents per roleMMLU-Pro accuracy (%)Total tokens per question (K)
CLIC, N=10268.029.8
CLIC, N=20469.154.6

Table R4 shows that doubling the team raises total tokens by only 1.83x, not 2x. Per agent, the cost goes down from 2.98K to 2.73K tokens (about 8% less), which agrees with the complexity argument that per-agent cost does not grow with N. Accuracy is maintained and slightly improves (68.0 to 69.1) with a controller that was never retuned for twenty agents. With 350 outcomes we do not claim the +1.1 itself is significant; the point is that CLIC scales to four times the primary team size without any degradation. Together with Table 9 the trend is consistent: from 5 to 10 agents Full Mesh tokens grow 2.25x (27.3K to 61.4K) while CLIC grows 1.87x (16.4K to 30.6K), and the token reduction rises from 39.9% to 50.2%. The saving gets larger as the team grows, which is exactly the regime the paper is motivated by.

We hope the new results on a current backbone, the significance tests, the per-seed breakdown and the scaling experiment address the soundness concerns. We are happy to run any further check the reviewer finds useful.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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