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Paper summary
This paper presents a comparative learning-theoretic framework for single-agent and multi-agent learning, focusing on three factors: statistical complexity, objective alignment, and error propagation. The authors derive PAC sample complexity bounds showing that independent task decomposition can reduce sufficient sample budgets, while dependent modular policies can match single-agent bounds under specific assumptions. They further quantify the effects of reward mismatch and policy-class differences, and analyze how local learning errors propagate through sequential agents. Exact Gaussian regression examples demonstrate that error amplification depends on coupling strength rather than merely agent count or dependency structure. Experiments on synthetic regression tasks and GSM8K using Qwen2.5-1.5B-Instruct provide qualitative support, showing that multi-agent learning tends to benefit independent tasks, whereas single-agent learning performs better on dependent tasks under the evaluated settings.
Critical strengths
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Systematic theoretical framework. The paper provides a structured analysis of single-agent and multi-agent learning by separating statistical complexity, objective alignment, and error propagation. This distinction is valuable because it clarifies the conditions under which task decomposition can improve learning efficiency and avoids attributing performance differences solely to agent count.
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Insightful analysis of error propagation. The exact Gaussian regression results demonstrate that error amplification can remain bounded or grow quadratically with agent count, even under the same dependency graph. This provides a meaningful theoretical insight into how coupling strength and downstream sensitivity, rather than dependency structure alone, determine learning difficulty.
Critical weaknesses
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Limited theoretical novelty and practical applicability. Most theoretical results build on established tools such as covering numbers, uniform convergence, and existing error propagation analyses. Moreover, the PAC bounds assume exact conditional-value access and global empirical optimization, excluding rollout costs, reward estimation errors, and practical optimization challenges. These limitations weaken both the originality and practical significance of the theoretical contributions.
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Insufficient empirical validation of the theoretical claims. The synthetic and GSM8K experiments provide only qualitative support without directly measuring key theoretical quantities such as reward mismatch or downstream error amplification. Furthermore, the absence of comparisons between joint and stagewise training makes it difficult to isolate the effects of task decomposition from differences in training procedures and policy classes. Consequently, the experiments do not convincingly establish the proposed framework's explanatory or predictive value.
Questions for authors
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Theoretical novelty: Which theoretical results represent substantive advances beyond existing covering-number, uniform convergence, and imitation-learning error propagation analyses? Clarifying the novelty of the main theorems would materially affect my assessment of the paper's contribution.
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Practical relevance: Given that the PAC analysis assumes exact conditional-value access and global empirical optimization, how should the resulting sample complexity comparisons be interpreted in practical RL settings with finite rollouts and estimated rewards? Could accounting for these costs change the relative efficiency conclusions?
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Empirical validation: Can the authors provide controlled comparisons between monolithic, jointly trained modular, and stagewise-trained modular policies under matched resources, and directly examine how local errors and downstream amplification vary with coupling strength? Such evidence would help determine whether the observed differences genuinely arise from the proposed theoretical mechanisms.
6 comments
Rebuttal (2/3)
Q2: Practical relevance and finite-rollout costs
Response. Thank you for this question. Our PAC analysis assumes access to the conditional expected reward for each sampled prompt and candidate policy . In practice, GRPO generates multiple rollouts to obtain sampled rewards for policy updates, including group-relative advantage estimates. These samples can also be used to estimate conditional expected rewards. Finite rollouts therefore introduce value-estimation error even when each response's reward is evaluated exactly.
Accounting for finite rollouts and approximate optimization. Proposition J.2 separates these errors from the statistical error due to sampling prompts. Let be the exact conditional-value objective averaged over the sampled prompts, and let be its estimated counterpart. Suppose
\qquad \widetilde J_n(\widehat\pi)\ge\sup_{\pi\in\Pi}\widetilde J_n(\pi)-\tau.$$ Here $\nu$ bounds estimation error uniformly over the policy class, and $\tau$ measures the optimization shortfall for that estimated objective. On the original uniform-convergence event $\sup_{\pi\in\Pi}|J(\pi)-\widehat J_n(\pi)|\le\epsilon_{\rm stat}/2$, Proposition J.2 gives $$\sup_{\pi\in\Pi}J(\pi)-J(\widehat\pi) \le\epsilon_{\rm stat}+2\nu+\tau.$$ If the statistical, estimation, and optimization events have failure probabilities $\delta_{\rm s}$, $\delta_{\rm v}$, and $\delta_{\rm o}$, the bound holds with probability at least $1-\delta_{\rm s}-\delta_{\rm v}-\delta_{\rm o}$. Thus, for target regret $\epsilon$, the original prompt bounds apply at statistical tolerance $\epsilon-2\nu-\tau>0$, with confidence allocated across the three events. **What this preserves.** Under the same policy-class, feedback, and factorization assumptions, the statistical bounds retain their dependence on policy complexity and task decomposition. For example, if $2\nu+\tau\le\rho\epsilon$ for a common fixed $0\le\rho<1$, each sufficient prompt bound applies at tolerance $(1-\rho)\epsilon$. The same structural criteria can then be used to compare learners at this reduced tolerance. Reward-transfer and class-optimum-gap terms remain applicable when comparing different objectives or policy classes. A concrete finite-policy example illustrates the rollout cost. For a class of $M$ policies fixed independently of the prompts and rollout draws, average $m$ rollout rewards per policy per prompt. If these rewards lie in $[0,1]$ and, for each policy, are independent conditional on the prompts, then $$\nu\le\sqrt{\frac{\log(2M/\delta_{\rm v})}{2nm}}$$ with conditional probability at least $1-\delta_{\rm v}$, using $Mnm$ evaluation rollouts. The bound is uniform over this finite class; any cost of training the candidates is additional. This illustrates how controlling value-estimation error requires resources beyond the prompt budget. Applying the calculation to GRPO's adaptive sampling requires a separate estimator analysis. **Connection to practical training cost.** Using the same RL algorithm, such as GRPO, under matched nominal training settings helps control the practical comparison. Our GSM8K experiments use the same GRPO configuration, including eight completions per group, across the compared learners. The reported task-dependent performance trends are qualitatively consistent with our analysis under finite sampling and approximate optimization.Rebuttal (3/3)
Q3/W2: Controlled empirical validation
Response. Thank you for the suggestions. We completed the three-way neural comparison and two Gaussian checks. Each Gaussian check used 30,000 simulated training datasets. The neural comparison examines task-dependent rankings; the Gaussian checks test quantitative predictions about amplification and class restriction.
1. Controlled comparison of training procedures
Setup. We compared monolithic, jointly trained modular, and stagewise modular learners across five seeds, couplings , and training sizes . Each model has approximately 33,000 parameters. The modular learners share their architecture and paired initialization, but train on generated histories (joint) or reference histories (stagewise). All learners use the same validation-only hyperparameter search.
Results. At , test excess MSE was (mean standard deviation across five seeds; lower is better):
| Coupling | Monolithic | Joint modular | Stagewise modular |
|---|---|---|---|
| 0 | |||
| 0.5 | |||
| 1 |
What this supports. Modular learners have lower mean error at zero coupling, while the monolithic learner has lower mean error at positive coupling. This qualitatively supports the framework's task-dependent comparison of decomposition. Joint training also has lower mean error than stagewise training at positive coupling, addressing the requested comparison within a fixed architecture. Model size and tuning are controlled, but computation is not equated, and the monolithic comparison changes the function class.
2. Gaussian check: shared downstream amplification
Setup. In the known-coupling model of Proposition 3.9, we compared matched stagewise, joint modular, and structured monolithic estimators (8 coefficients each) with unrestricted monolithic OLS (32 coefficients). All receive the same complete trajectories. We used , , , , and coupling strength .
Results. The three structured estimators coincide, and their local excess MSE stays at . Monte Carlo results agree with the following exact complete-output excess risks:
| Coupling | Each structured learner | Unrestricted monolithic |
|---|---|---|
| 0 | 0.0328 | 0.1455 |
| 1 | 0.0624 | 0.2768 |
| 2 | 0.2969 | 1.3172 |
What this supports. As dependence becomes stronger, overall prediction error increases even though local estimation error stays the same. This supports Proposition 3.9 by showing that stronger dependence amplifies the effect of local errors, including under joint training. The three structured learners remain equally accurate and outperform the unrestricted monolithic learner at every tested coupling strength.
3. Gaussian check: when feature restriction helps
Setup. We tested the separate Appendix J.8 example with , , , and , changing edge strength while fixing the graph topology and feature classes.
Results. The restricted-minus-full excess risk was:
| Coupling | Exact prediction | Monte Carlo mean [95% interval] |
|---|---|---|
| 1 | −0.0525 | −0.0527 [−0.0593, −0.0460] |
| 2 | 0.0350 | 0.0357 [0.0204, 0.0510] |
What this supports. Using fewer features reduces error at but increases it at , as predicted by Proposition J.6. At weaker coupling, the benefit of estimating fewer parameters outweighs the loss of useful information. Stronger coupling makes that information more important for downstream predictions, reversing the advantage in this example.
These simulations check the predicted Gaussian errors; the independent minimax result in Q1 is established by a separate proof. Joint and stagewise learners coincide in the Gaussian comparison because they optimize the same likelihood. The neural learners use different objectives, and their results do not directly test PAC rates. Further measurements on the fitted neural models are needed to determine whether error propagation explains their ranking reversal.
Manuscript changes. We added the neural setup and results in Appendix H.5.1 (Table 2), the matched Gaussian risk predictions and Monte Carlo checks in Appendix J.7.2 (Tables 4–5), and the feature-restriction simulation in Appendix J.8.1 (Table 7). All additions, including the tables and captions, are highlighted in red.
In the end, thank you again for your thoughtful feedback. We hope our responses address your concerns, and we would be happy to clarify any remaining points or discuss further questions.
Rebuttal (1/3)
Thank you for your detailed and thoughtful review. We appreciate the opportunity to address your questions and concerns. Below, we clarify our theoretical contribution, explain how finite rollouts and approximate optimization affect the comparison, and present additional controlled experiments.
Response. Thank you for raising this concern. We agree that the distinction between established proof tools and the contribution of our analysis should be clearer.
1. Our contribution: answering when task decomposition helps learning.
Our work addresses a meaningful open question in agent-system design: when does task decomposition improve learning efficiency, and when do its costs offset its benefits? Decomposition can simplify local learning while changing the training objective, restricting attainable performance, and introducing downstream sensitivity to errors. Understanding its benefit therefore requires comparing these effects together.
Our contribution is a conditional theoretical answer under explicit observation models and performance targets. We characterize when specialization improves sufficient learning guarantees, when dependent modular learning can match a single learner, and when downstream sensitivity reverses the benefit of restricting local models. The contribution lies in these comparative conclusions and the conditions that support them.
2. Why answering this question requires a comparative framework.
Existing guarantees concern different quantities: generalization bounds typically compare learners with their class optima; reward-transfer bounds account for objective changes; and propagation bounds alone do not specify how local errors decrease with data. Comparing them requires reconciling observation models, objectives, and performance comparators.
A smaller class, for example, may yield a better estimation bound but a worse optimal task reward. Likewise, downstream amplification need not disadvantage modular learning if a matched single learner shares the same sensitivity. Our framework makes these distinctions explicit, identifying how factorization, information access, and training procedures affect the benefits of decomposition.
3. Concrete answers established by the analysis.
When can specialization improve the learning guarantee? Under independent policy and reward factorization, Cartesian trainable parameters, and local-value access, Theorem 3.3 gives a sufficient prompt budget governed by the largest local complexity. Propositions 3.4 and 3.7 specify when this improves the comparison with a single learner. With reward discrepancy α and a nonnegative bound a on the relevant class-optimum gap, the transferred guarantee uses the remaining tolerance ε−a−2α>0. Thus, complexity savings must be assessed together with objective distortion and lost expressivity. A single learner with the same factorization and feedback shares the structural benefit.
Does dependence necessarily impose an additional learning penalty? Proposition 3.5 shows that dependent modular policies can match the single-agent sufficient budget when dimension, radii, and segment regularity are matched and the complete return is optimized jointly. Separately, Proposition 3.9 gives an exact Gaussian comparison: with known coupling, stagewise least squares and matched joint likelihood estimation yield the same estimator and expected excess MSE. Two coupling families with the same dependency-graph topology exhibit bounded versus quadratic amplification in the number of stages K. This identifies sensitivity shared by both learners and shows why connectivity alone does not determine learning requirements.
When can dependence overturn the benefit of a smaller local model? Proposition J.6 in Appendix J.8 gives the exact criterion
\quad\Longleftrightarrow\quad \bar b_G(n-p-1)\le\sigma^2(p-q), \qquad n>p+1.$$ Here $p$ and $q<p$ are the full and retained feature dimensions, and $\bar b_G$ weights omitted signal by its downstream sensitivity. The insight is that **where information is discarded matters**: changing coupling changes the relative cost of omitted information at different stages. Table 6 shows that changing one edge strength reverses the preferred class while fixing the graph, feature classes, and sample size. This reversal persists after normalization by Bayes MSE.Additional tightness result established for the rebuttal. Proposition J.5 in Appendix J.7.1 provides matching upper and lower bounds for independent Gaussian prediction from complete trajectories. Modular estimation and a structured single learner with the same class and information both attain the minimax expected excess MSE. The addition is included in the revised manuscript and highlighted in red.