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Under review as a conference paper at ICLR 2027

Understanding Single- and Multi-Agent Learning: Complexity, Alignment, and Error Propagation

Abstract

When does decomposing a task across specialized agents improve learning efficiency? Empirical studies report mixed outcomes across tasks, training procedures, and resource budgets. We develop a comparative learning-theoretic framework for monolithic and modular sequential policies, organizing established tools around three mechanisms: statistical class complexity, objective and policy-class mismatch, and stagewise learning errors. Under conditional-value access, independent policy and reward factorization yields a local-complexity guarantee; dependent modular policies can match the single-agent sufficient budget under matched dimension, horizon, and radius allocations. Reward discrepancy and class-optimum gaps qualify these comparisons, while a separate reference-demonstration analysis relates local learning rates to downstream error propagation. Finite-class and exact Gaussian regression examples show why neither agent count nor dependency graph alone determines learning costs. The framework makes explicit the observation models and comparators needed to attribute efficiency differences to decomposition. Its PAC results compare sufficient budgets, while the regression example gives exact expected excess risks under stated assumptions.

Primary area:
learning theory
Keywords:
agent system, sample complexity

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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_TW9zOpenReview ↗
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2
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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
  1. 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.

  2. 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
  1. 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.

  2. 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
  1. 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.

  2. 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?

  3. 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
AuthorsOpenReview ↗

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.

Q1/W1: Theoretical novelty and contribution

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\alpha and a nonnegative bound aa on the relevant class-optimum gap, the transferred guarantee uses the remaining tolerance ε−a−2α>0\varepsilon-a-2\alpha>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 KK. 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.

AuthorsOpenReview ↗

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 fπ(x)=EY∼π(⋅∣x)[R(x,Y)]f_\pi(x)=\mathbb E_{Y\sim\pi(\cdot\mid x)}[R(x,Y)] for each sampled prompt xx and candidate policy π\pi. 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 J^n\widehat J_n be the exact conditional-value objective averaged over the nn sampled prompts, and let J~n\widetilde J_n 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.
AuthorsOpenReview ↗

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 λ∈{0,0.5,1}\lambda\in\{0,0.5,1\}, and training sizes n∈{100,400,1600}n\in\{100,400,1600\}. 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 n=400n=400, test excess MSE was (mean ±\pm standard deviation across five seeds; lower is better):

Coupling λ\lambdaMonolithicJoint modularStagewise modular
00.1748±0.00280.1748 \pm 0.00280.0629±0.00300.0629 \pm 0.00300.0626±0.00310.0626 \pm 0.0031
0.50.1788±0.00250.1788 \pm 0.00250.1941±0.00380.1941 \pm 0.00380.2021±0.00460.2021 \pm 0.0046
10.1845±0.00240.1845 \pm 0.00240.2372±0.00410.2372 \pm 0.00410.2404±0.00510.2404 \pm 0.0051

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 K=4K=4, p=2p=2, n=64n=64, σ2=1\sigma^2=1, and coupling strength c∈{0,1,2}c\in\{0,1,2\}.

Results. The three structured estimators coincide, and their local excess MSE stays at 0.03280.0328. Monte Carlo results agree with the following exact complete-output excess risks:

Coupling ccEach structured learnerUnrestricted monolithic
00.03280.1455
10.06240.2768
20.29691.3172

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 K=2K=2, p=2p=2, q=1q=1, and n=8n=8, changing edge strength cc while fixing the graph topology and feature classes.

Results. The restricted-minus-full excess risk was:

Coupling ccExact predictionMonte Carlo mean [95% interval]
1−0.0525−0.0527 [−0.0593, −0.0460]
20.03500.0357 [0.0204, 0.0510]

What this supports. Using fewer features reduces error at c=1c=1 but increases it at c=2c=2, 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.

Reviewer_ZYrvOpenReview ↗
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Paper summary

This paper develops a learning-theoretic framework for comparing single-agent (SARL) and modular multi-agent (MARL) policies. It examines three mechanisms: (1) statistical complexity under independent and dependent task decomposition, (2) reward and policy-class mismatch, and (3) stagewise error propagation. The analysis derives PAC sufficient sample budgets, quantifies the impact of reward misalignment, and establishes error-propagation bounds. Exact Gaussian regression examples further demonstrate that learning costs depend on coupling strength rather than agent count or dependency structure alone. Synthetic regression and GSM8K experiments provide empirical illustrations.

Critical strengths
  1. Systematic theoretical framework. The paper clearly distinguishes statistical complexity, objective mismatch, and error propagation, providing a useful perspective on when task decomposition may improve learning efficiency.
  2. Careful treatment of assumptions. The authors explicitly distinguish sufficient sample budgets from minimal sample complexity and clarify the different observation models and performance comparators.
  3. Interesting analytical insights. The dependent-policy analysis shows that a quadratic penalty in agent count is not inevitable, while the exact Gaussian examples demonstrate how coupling strength influences error amplification and the estimation–approximation trade-off.
Critical weaknesses
  1. Limited theoretical novelty. Most results rely on established techniques, including covering-number generalization bounds, reward-transfer inequalities, imitation-learning error propagation, and Gaussian regression analysis. The genuinely new theoretical contributions beyond combining these existing results are not sufficiently clear.
  2. Limited conclusions about actual sample efficiency. The main PAC results compare sufficient upper bounds rather than minimal sample complexities. Consequently, they do not establish that decomposition intrinsically improves learning efficiency. In particular, the independent-case advantage appears to arise primarily from policy-class factorization rather than the use of multiple agents.
  3. Strong and unrealistic theoretical assumptions. The PAC analysis assumes exact conditional-value access, exact empirical optimization, and uniform Lipschitz parameterization. These assumptions substantially limit its applicability to practical LLM reinforcement learning, where rollout estimation and optimization costs are central.
  4. Weak connection between theory and experiments. The GRPO experiments do not directly instantiate the theoretical observation models. Key quantities such as reward discrepancy, policy-class gaps, and local policy errors are not measured. Thus, the experiments provide only qualitative support for the proposed mechanisms.
  5. Insufficient experimental details and potentially confounded comparisons. Some hyperparameter settings are unspecified, and Appendix H.5 describes proposed rather than executed protocols. Furthermore, matching trainable parameter counts does not necessarily ensure comparable rollout or computational budgets. The GSM8K task constructions also introduce differences in problem structure and generation requirements.
Questions for authors
  1. What are the main theoretical contributions beyond applying established generalization, reward-transfer, and imitation-learning results to factorized sequential policies?
  2. Can the authors provide tighter bounds, lower bounds, or a separation result demonstrating when decomposition genuinely reduces minimal sample complexity, rather than only its sufficient upper bound?
  3. How would the conclusions change under realistic finite-rollout reward estimation and approximate optimization? Can the framework provide meaningful guarantees for practical LLM-RL training?
  4. Can the authors empirically measure or approximate the theoretical quantities, particularly reward discrepancy, policy-class gaps, and stagewise errors, and correlate them with observed performance?
  5. Can the authors clarify the executed experimental protocols and report complete hyperparameters, variability across seeds, and matched rollout, token, and computational budgets? A factorized single-agent baseline would also help isolate the benefits of decomposition from those of multi-agent architecture.
6 comments
AuthorsOpenReview ↗

Rebuttal (1/4)

Thank you for your detailed and thoughtful review. Your questions helped us clarify the contribution. We appreciate the opportunity to address each question together with the related concern.

Q1 and W1. Theoretical contributions

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.

Established results provide essential ingredients, but their guarantees concern different quantities. Generalization bounds typically compare a learner with its own class optimum; reward-transfer bounds account for changes in the objective; and a propagation inequality alone does not specify how local errors decrease with training data. Comparing these guarantees requires reconciling their observation models, objectives, and performance comparators.

For example, a smaller policy class may have a better estimation bound while attaining a worse optimal task reward. Likewise, downstream error amplification does not establish a disadvantage of modular learning if a matched single learner experiences the same sensitivity. Our framework makes these distinctions explicit, allowing us to identify which apparent benefits come from factorization, information access, or the learning procedure. This comparative analysis connects established tools to the agent-design question.

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\alpha and a nonnegative bound aa on the relevant class-optimum gap, the transferred guarantee uses the remaining tolerance ε−a−2α>0\varepsilon-a-2\alpha>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 KK. 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.
  • 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. This addition is highlighted in red in the updated manuscript.

AuthorsOpenReview ↗

Rebuttal (2/4)

Q2: tighter bounds, lower bounds, or a separation result demonstrating when decomposition genuinely reduces minimal sample complexity

Response. Thank you for this question. We have added a matching lower bound in an independent Gaussian model, establishing the exact minimax sample requirement. Both modular learning and a structured single learner attain this requirement, clarifying when their sufficient guarantees are optimal.

An exact minimax comparison. Consider KK independent subtasks Yi=wi⊤xi+ξi,Y_i=w_i^\top x_i+\xi_i, with unrestricted wi∈Rpw_i\in\mathbb R^p, p≥1p\ge1, known σ2>0\sigma^2>0, and mutually independent xi∼N(0,Ip)x_i\sim N(0,I_p) and ξi∼N(0,σ2)\xi_i\sim N(0,\sigma^2). Both learners use the same product linear class and receive the same n>p+1n>p+1 independent complete observations, each containing all KK labels. Proposition J.5 establishes inf⁡f^sup⁡W1KE∣f^(X)−fW(X)∣22=σ2pn−p−1.\inf_{\widehat f}\sup_W \frac1K\mathbb E\lvert \widehat f(X)-f_W(X)\rvert_2^2 =\frac{\sigma^2p}{n-p-1}. where fW(X)=(wi⊤xi)i=1Kf_W(X)=(w_i^\top x_i)_{i=1}^K, and the expectation includes training data and a fresh test input. The lower bound applies to arbitrary estimators and follows from Gaussian coefficient priors with variance tending to infinity. Local least squares and matched joint estimation attain it.

Consequently, for normalized expected excess MSE ϵ>0\epsilon>0, the modular sufficient budget and the single-learner necessary budget coincide:

=p+1+\left\lceil\frac{\sigma^2p}{\epsilon}\right\rceil.$$ Under this complete-observation convention, the optimal requirement depends on the local dimension $p$, although the total parameter dimension is $Kp$. A single learner using the same factorization and information shares this benefit. **Scope of the result.** This establishes tightness in the Gaussian prediction setting. Extending it to the broader PAC comparison requires a separate lower-bound analysis: the PAC results concern compact parameter classes, exact conditional-value feedback, and high-probability reward regret. Compactness and Lipschitz regularity alone do not ensure the class richness needed for a matching lower bound. Comparisons across different classes must also account for differences in their best attainable task performance. **Manuscript changes.** Appendix J.7.1 now includes Proposition J.5, its full proof, and the matching sample budgets in equations (J.5)–(J.6). The additions and scope clarifications are highlighted in red. > **W2: upper bounds comparison** **Response.** Thank you for this insightful comment. We agree with both points. As acknowledged in Section 3.2 and Appendix I.3, our PAC results compare **worst-case sufficient guarantees**. Comparing these upper bounds does not establish which paradigm has lower actual risk or minimal sample complexity. **Factorization and agent count.** The independent-case benefit comes from policy-class factorization and local-value access under the theorem's assumptions. A single learner with the same class, information, and objective shares this benefit. The new Appendix J.7.1 complements this observation: in the Gaussian complete-observation model, modular and matched structured single learners have the same minimax sample requirement for expected excess MSE. **Why the comparison remains useful.** The framework identifies how decomposition affects the guarantees: restricting a class can reduce the estimation term while losing expressive power, local rewards can differ from the task objective, and early errors can affect later outputs. We account for these effects under explicit observation models and performance targets, matching PAC accuracy and confidence levels and allowing for class-optimum gaps. [1] study factorization through regret bounds, while [2] bound compounding prediction errors. These works motivate studying structural effects through guarantees; they do not establish tightness or an architectural separation for our setting. [1] Efficient Reinforcement Learning in Factored MDPs with Application to Constrained RL [2] Efficient Reductions for Imitation Learning
AuthorsOpenReview ↗

Rebuttal (3/4)

Q3 and W3. Finite rollouts and approximate optimization

Response. Thank you for this question. Our PAC analysis assumes access to the exact conditional expected reward fπ(x)=EY∼π(⋅∣x)[R(x,Y)]f_\pi(x)=\mathbb E_{Y\sim\pi(\cdot\mid x)}[R(x,Y)] for each sampled prompt and candidate policy. Proposition J.2 extends the analysis to estimated rewards and approximate optimization by explicitly accounting for their errors.

1. Accounting for estimation and optimization errors. Let J^n\widehat J_n denote the exact conditional-value objective averaged over nn prompts, and J~n\widetilde J_n its estimated counterpart. Suppose

\qquad \widetilde J_n(\widehat\pi)\ge\sup_{\pi\in\Pi}\widetilde J_n(\pi)-\tau.$$ Here $\nu$ bounds estimation error uniformly over the policy class, while $\tau$ measures the optimization shortfall. On the original uniform-convergence event $\sup_{\pi\in\Pi}|J(\pi)-\widehat J_n(\pi)|\le\epsilon_{\rm stat}/2$, Proposition J.2 gives $$\sup_{\pi\in\Pi}J(\pi)-J(\widehat\pi) \le\epsilon_{\rm stat}+2\nu+\tau.$$ If these three events have failure probabilities $\delta_{\rm s}$, $\delta_{\rm v}$, and $\delta_{\rm o}$, respectively, the guarantee holds with probability at least $1-\delta_{\rm s}-\delta_{\rm v}-\delta_{\rm o}$. Thus, achieving regret $\epsilon$ requires applying the original prompt bounds at statistical tolerance $\epsilon-2\nu-\tau>0$. **2. Implications for the main comparisons.** The main PAC comparisons remain applicable when these errors are controlled and the remaining assumptions hold. If both learners satisfy $2\nu+\tau\le\rho\epsilon$ for a common fixed $0\le\rho<1$, their sufficient prompt bounds can be compared at tolerance $(1-\rho)\epsilon$ and a common statistical confidence level. At this reduced tolerance, the independent-case bound retains its dependence on the largest local complexity, and the dependent-case budget matches the single-learner budget under the stated matching conditions. The original budget-comparison criteria apply at this adjusted tolerance. Comparisons across different rewards or policy classes must additionally account for reward mismatch and class-optimum gaps. **3. A concrete finite-rollout example.** For $M$ policies fixed in advance, draw $m$ independent $[0,1]$ reward samples per policy per prompt, conditional on the prompts. Averaging these samples gives $$\nu\le\sqrt{\frac{\log(2M/\delta_{\rm v})}{2nm}}$$ with probability at least $1-\delta_{\rm v}$, using $Mnm$ rollouts. This provides an explicit way to control estimation error. Retaining the comparison guarantees also requires controlling the optimization shortfall; additional rollouts alone do not ensure this. Establishing both error controls for adaptive GRPO remains future work. >**Q4 and W4. Measuring discrepancies and stagewise errors** **Response.** Thank you for these comments. We agree that the GRPO experiments provide qualitative evidence consistent with the mechanisms studied, but do not directly instantiate our theoretical observation models. We respectfully ask that the paper be evaluated primarily for its theoretical contribution to comparing single-agent and multi-agent learning. To examine the mechanisms more directly, we conducted the following controlled experiments. **1. Stagewise errors and downstream performance.** In a separate controlled experiment, we measured prediction errors under reference and generated histories. We then replaced the first generated output with its noiseless conditional mean to assess the effect on later predictions. This intervention provides quantitative evidence of downstream sensitivity to early errors. It does not isolate how much propagation explains the differences between training methods or directly measure the policy-distance quantities in the imitation-learning analysis. The updated overall performance comparison is reported in [Q5/W5](#q5). **2. Known class-optimum gaps in the Gaussian control.** In Appendix J.8, the generator allows us to calculate the gap between the restricted and full classes' optimal expected excess MSE: $0.255$ at $c=1$ and $0.630$ at $c=2$. With the graph, feature classes, and sample size fixed, simulations reproduce the predicted reversal: the restricted OLS estimator performs better at $c=1$ and worse at $c=2$. This supports the predicted tradeoff between estimation savings and approximation loss. **3. Remaining measurements.** Neural class-optimum gaps depend on each class's best attainable reward, which fitted-model scores alone cannot establish. Policy-distance errors require information about the reference policy's output distribution beyond ground-truth answers. These challenges motivate controlled models with known quantities. Policy-specific expected reward discrepancy can be estimated by scoring held-out outputs under both rewards with the same policy and decoding rule; this measurement remains pending.
Reviewer_vzKjOpenReview ↗
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Paper summary

This paper investigates when decomposing a complete task into specialized agents can reduce the amount of training data required to achieve the same task performance. The authors develop a theoretical framework comparing single-agent and modular multi-agent learning through policy-class complexity, reward and policy-class mismatch, and the propagation of stagewise learning errors. The theoretical results show that decomposition can reduce sufficient sample budgets under independence and objective-alignment conditions, while dependent modular policies can match the single-agent budget guarantee under appropriately matched conditions. The stagewise analysis and exact Gaussian regression examples further demonstrate that overall learning difficulty depends on local learning rates and downstream error amplification, rather than agent count or the dependency graph alone. Synthetic regression and GSM8K experiments exhibit trends favoring multi-agent learning on independent tasks and single-agent learning on dependent tasks under the evaluated configurations, providing qualitative support for the framework without establishing a universal ranking of the two architectures.

Critical strengths

The paper addresses a practically relevant research question. The paper examines when task decomposition can improve training-data efficiency, addressing inconsistent findings in comparisons between single-agent and multi-agent systems. Beyond comparing final task performance, this perspective considers the learning cost required to attain that performance. Framing the discussion around conditional benefits and costs helps formulate more specific research questions.

The framework clearly separates the main mechanisms affecting learning efficiency. The paper distinguishes statistical complexity, reward and policy-class mismatch, and downstream propagation of local learning errors, rather than attributing all effects to agent count. In particular, separating reward mismatch from limitations in policy-class expressivity gives objective distortion and loss of attainable performance distinct analytical roles. This separation provides a clear conceptual structure for organizing and interpreting modular learning problems.

The theoretical analysis explicitly states the conditions under which different results apply. The authors distinguish information models such as conditional-value access and reference demonstrations, specifying the corresponding objectives and performance comparators. The paper also clarifies that sufficient sample budgets do not characterize minimal sample complexity and that the theoretical results do not directly establish convergence guarantees for practical optimizers. These scope statements help readers interpret the theorems accurately and reduce the risk of extrapolating idealized results directly to practical training.

The exactly solvable regression examples offer useful mechanistic insights. Under explicit Gaussian model assumptions, the authors separate local estimation error from downstream amplification, allowing their effects to be calculated directly. The examples show that the same dependency graph can exhibit different degrees of error amplification under different coupling strengths. Comparisons between restricted and full feature classes further illustrate the trade-off between estimation savings and the cost of omitted information. Together, these results provide concrete illustrations of why parameter count and connectivity alone are insufficient to determine learning performance.

Critical weaknesses

The paper primarily integrates established tools, including covering numbers, uniform convergence, reward-discrepancy transfer bounds, sequential error propagation, and Gaussian regression analysis, with much of its contribution residing in a unified comparative framework. The derivations of the local-complexity benefit for independent tasks and the reward-mismatch correction are relatively direct, while the differing amplification rates under the same dependency graph are insightful but not sufficiently distinguished from existing theory. Consequently, the boundaries between conceptual synthesis, extensions of established results, and substantive new theoretical contributions remain unclear.

The PAC analysis assumes access to exact conditional expected rewards for candidate policies and an empirical objective maximizer, whereas practical training relies on finite rollout sampling and a finite number of optimization steps. Although the appendix decomposes statistical, value-estimation, and optimization errors, it does not establish corresponding error guarantees for the sampler and optimizer used in the experiments. It therefore remains unclear whether the statistical gains predicted under idealized conditions persist in practical GRPO training or are offset by additional sampling and optimization costs.

The independent GSM8K construction combines two unrelated questions, whereas the dependent construction divides a single question into reasoning and answering, simultaneously changing task composition, role allocation, and evaluation; the resulting performance reversal therefore cannot be attributed solely to dependence or error propagation. Moreover, the answering module receives both the original question and the upstream reasoning, allowing it to bypass or ignore the latter, so the degree of actual dependence remains unverified. The absence of interventions on upstream information limits the evidence supporting the proposed error-propagation explanation.

The appendix states that 512 questions are reserved from the official training split for validation and that the remaining questions are paired without reuse, with each pair constituting one complete training example. Given the official training split of 7,473 questions, this protocol permits at most 3,480 complete training examples, whereas Figure 1(e), with its “×50” horizontal-axis notation, appears to extend to approximately 5,000 examples. This discrepancy leaves the sample-counting unit and actual data-construction procedure unclear, complicating the interpretation of the sample-efficiency curves.

Questions for authors

Which results constitute substantive advances over existing theory, and what are the key technical challenges that go beyond direct applications of established tools? Could the authors distinguish conceptual synthesis, extensions of prior results, and new theoretical insights through explicit comparisons with the most closely related work?

Do the predicted statistical benefits of modularization persist under finite rollout sampling and approximate optimization? Could the authors provide more concrete theoretical or empirical evidence and report the numbers of rollouts, reward evaluations, and optimization updates required by single-agent and multi-agent systems to reach the same performance?

Could the authors test the answering module’s actual dependence on upstream reasoning by removing, shuffling, or controllably perturbing that reasoning under otherwise matched questions, model configurations, and evaluation metrics? What are the results of the reference-reasoning substitution diagnostic mentioned in the appendix, and do they support attributing the performance gap to upstream error propagation?

Could the authors explain the discrepancy between the approximately 5,000 examples shown in Figure 1(e) and the maximum of 3,480 complete training examples permitted by the stated pairing-without-reuse protocol? Does the horizontal axis count distinct question pairs, individual questions, or cumulative training exposures, and was question reuse allowed during data construction?

5 comments
AuthorsOpenReview ↗

Rebuttal (1/4)

Thank you for your thoughtful review. Our paper examines when task decomposition improves statistical learning efficiency and when its costs offset the benefits. We appreciate the opportunity to address your questions and related concerns in the following.

Q1 / W1. Theoretical contribution and relationship to prior work

Response. Thank you for raising this concern. We agree that the distinction between conceptual synthesis, adaptations of established results, and the comparative insights 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.

The technical challenge is to make guarantees with different observation models, objectives, and comparators meaningful for the same design question. A smaller class can have a better estimation bound while attaining a worse optimal task reward; downstream amplification can affect both modular and matched single learners. We distinguish the roles of prior results and our analysis as follows.

  • Conceptual synthesis. [1] derive a lower bound for goal-conditioned hierarchical RL, and [2] establish regret guarantees for factored MDPs. These works already quantify benefits of structure under environment interaction. Our framework compares policy-learning guarantees under conditional-value access and, separately, reference demonstrations, while accounting explicitly for reward mismatch, class-optimum gaps, and downstream sensitivity.

  • Adaptations of established results. The covering-number and reward-transfer arguments use standard tools. Theorem 3.8 adapts the sequential error-propagation principle of [3] to normalized segment rewards. We separate this execution bound from the local learning-rate premise needed to obtain demonstration budgets. This distinguishes the effect of dependence from the difficulty of learning each stage.

  • Comparative insights. Gaussian least-squares risk calculations are established [4]. We use them to determine which sensitivity is shared by matched learners and when downstream weighting of omitted information reverses the benefit of feature restriction. The explicit conditions and counterexamples below provide concrete answers to the decomposition question.

[1] Sample Complexity of Goal-Conditioned Hierarchical Reinforcement Learning

[2] Efficient Reinforcement Learning in Factored MDPs with Application to Constrained RL

[3] Efficient Reductions for Imitation Learning

[4] Two models of double descent for weak features

AuthorsOpenReview ↗

Rebuttal (2/4)

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\alpha and a nonnegative bound aa on the relevant class-optimum gap, the transferred guarantee uses the remaining tolerance ε−a−2α>0\varepsilon-a-2\alpha>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 KK. 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. This addition, highlighted in red, establishes tightness in the independent Gaussian model. It does not establish a lower bound for the broader conditional-value PAC setting or an intrinsic advantage of multiple agents.

AuthorsOpenReview ↗

Rebuttal (3/4)

Q2 / W2. Finite rollouts, optimization, and matched-performance costs

Response. Thank you for this question. Our PAC analysis assumes access to the conditional expected reward fπ(x)=EY∼π(⋅∣x)[R(x,Y)]f_\pi(x)=\mathbb E_{Y\sim\pi(\cdot\mid x)}[R(x,Y)] for each sampled prompt xx and candidate policy π\pi. 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 J^n\widehat J_n be the exact conditional-value objective averaged over the nn sampled prompts, and let J~n\widetilde J_n 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.$$ If the statistical, estimation, and optimization events have failure probabilities $\delta_{\rm s}$, $\delta_{\rm v}$, and $\delta_{\rm o}$, the bound holds with probability at least $1-\delta_{\rm s}-\delta_{\rm v}-\delta_{\rm o}$. Thus, for target regret $\epsilon$, the original prompt bounds apply at statistical tolerance $\epsilon-2\nu-\tau>0$, with confidence allocated across the three events. **What this preserves.** Under the same policy-class, feedback, and factorization assumptions, the statistical bounds retain their dependence on policy complexity and task decomposition. For example, if $2\nu+\tau\le\rho\epsilon$ for a common fixed $0\le\rho<1$, each sufficient prompt bound applies at tolerance $(1-\rho)\epsilon$. The same structural criteria can then be used to compare learners at this reduced tolerance. Reward-transfer and class-optimum-gap terms remain applicable when comparing different objectives or policy classes. A concrete finite-policy example illustrates the rollout cost. For $M$ policies fixed in advance, averaging $m$ conditionally independent $[0,1]$ rollouts per policy per prompt gives, conditional on the prompts, $$\nu\le\sqrt{\frac{\log(2M/\delta_{\rm v})}{2nm}}$$ with probability at least $1-\delta_{\rm v}$, using $Mnm$ rollouts. This illustrates how controlling value-estimation error requires resources beyond the prompt budget. **Connection to practical training cost.** Our comparison concerns statistical learning requirements under the stated training configurations. The GRPO hyperparameters specify the sampling and update procedure, while the theoretical extension accounts for the resulting estimation and optimization errors. Comparing total computational cost at matched performance is a separate question and is outside the efficiency claim studied here.

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