1. The learning experiments are not clearly aligned with the proposed algorithm
The method is presented as critic calibration without reward modification: Equations (9)–(11) introduce an interaction loss and retain a conventional actor advantage. In contrast, Section 4.1 describes “four matched reward conditions,” including equal-split rewards and observational Shapley credit, and Section 4.4 attributes results to “direct-interventional credit.”
It is therefore unclear whether observational Shapley is:
- a matched interaction-regularized critic using observational targets;
- an agent-specific reward redistribution method; or
- another actor-side credit mechanism.
These alternatives test different hypotheses. The paper needs explicit losses and actor updates for every condition. In particular, it should explain how equal-split rewards relate to the shared action critic and advantage in Equation (11). Without this information, the central performance comparison is not interpretable.
The statement that factual trajectories are held fixed “across all learning conditions” also requires clarification. Independently updated on-policy actors generally generate different trajectories. If trajectories are literally shared, the off-policy learning protocol must be specified; if only initial conditions and random seeds are matched, the wording should be corrected.
2. The causal motivation is not connected convincingly to the downstream benchmark
The SCM deliberately includes an omitted common cause of actions and outcomes. That establishes a possible observational/interventional distinction, but not its relevance to the evaluated on-policy MPE setting.
For independently randomized decentralized policies, conditioning on the histories determining those policies ordinarily removes action–outcome confounding, provided policy randomization is exogenous. Under those conditions, an observational action critic marginalized using the matching policy kernel can already represent the proposed intervention response. Correlation among agents’ actions alone does not establish residual confounding.
The authors should identify the actual omitted variable or assignment mechanism producing a causal discrepancy in their MPE experiments, and measure that discrepancy directly. Otherwise, the gains could reflect additional rollout supervision or generic critic regularization rather than correction of causal bias. The synthetic deconfounding result does not resolve this question.
3. Baselines and ablations do not isolate the contribution
The evaluation lacks sufficiently strong, clearly specified comparisons. A normalized “team reward” reference is not an adequate description of the underlying learner, implementation, and tuning.
Critical missing comparisons include:
- The identical action-critic/MAPPO pipeline with λICR=0.
- Observational and interventional interaction teachers used in otherwise identical critic losses.
- Direct interventional return supervision without Shapley interaction aggregation.
- A compute- or environment-interaction-matched baseline using the additional teacher rollout budget.
- Ablations over interaction order, queried pairs, regularization strength, teacher accuracy, and teacher refresh frequency.
- Relevant implemented credit-assignment baselines, rather than treating a custom observational-Shapley condition as representative of the cited methods.
The extra simulator access is especially important: improvements of approximately 4–7% cannot be attributed specifically to causal interaction consistency without accounting for additional information and training cost.
4. Experimental reporting is inadequate for reproduction or statistical assessment
The supplied paper does not specify essential details, including:
- SCM structural equations, parameters, and outcome construction.
- Number of training seeds and uncertainty-estimation procedure.
- Network architectures, optimizer settings, training horizon, and PPO hyperparameters.
- Return targets, discounting, interaction weights, and regularization coefficients.
- Teacher rollout horizons, number of histories queried, continuation-policy snapshots, and refresh schedule.
- Concrete cross-fitting or lagged-teacher implementation.
- Simulator reset procedure and treatment of latent state when conditioning on a history.
- Absolute returns, normalization formulas, and numerical teacher-query or wall-clock costs.
The reported normalized AUC and final-return ratios also need precise definitions. Simple Spread commonly uses negative returns, so a ratio above one does not automatically mean better performance. Any sign reversal, shifting, or other transformation must be stated. The supplied reporting does not allow a reliable assessment of whether the modest gains exceed training variability.
5. The support audit conflates different notions of support
The paper alternates between action legality, behavior-policy support, and causal validity. A legal intervention need not have positive probability under the current behavior policy when a simulator can execute it directly; observational positivity is a separate requirement.
Moreover, standard finite-logit softmax policies assign positive probability to all unmasked discrete actions. The claimed 50–61% “zero-support” rates therefore require an explicit explanation: are these masked actions, thresholded probabilities, empirical non-occurrence, or genuinely impossible joint assignments? Standard Simple Spread also does not explain the claimed mask structure by itself.
Sampling from the policy makes zero behavior-support violations largely true by construction. This does not independently establish a better causal estimator. Likewise, the compared complement kernels define different coalition games, so lower “plan variance” needs a precise definition and an accuracy comparison, not just a relative variance figure.
6. The theoretical contribution is limited
Proposition 1 follows immediately from a zero weighted squared loss and exact targets. Strictly, an expectation of zero establishes equality almost surely under the evaluation distribution, rather than an unrestricted pointwise guarantee. Proposition 2 essentially assumes that the observational/interventional discrepancy survives the selected contrast and concludes that the contrast differs.
These observations are useful clarifications but offer little substantive analysis of the practical algorithm. There is no finite-sample interaction error bound, treatment of teacher noise or policy drift, or analysis of the trade-off between factual return prediction and causal calibration. Such analysis would strengthen the contribution considerably.
7. Error:
Proposition 2 incorrectly infers nonzero critic interaction-consistency loss from a surviving observational-versus-interventional coalition contrast. Observational conditioning on a coalition is not generally the same as marginalizing the optimal full-action observational critic with the declared complement kernel. The counterexample above satisfies the stated discrepancy condition while every observationally optimal critic has zero interaction-consistency loss. Location: Section 3.5, Proposition 2 on page 6 and its proof sketch on page 7; relevant definitions are Equations (2), (4), and (7).