- Rating
- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
Read review
Paper summary
The paper proposes STARS, a scheduling layer for synchronous agentic RL rollouts. A platform-profiled simulator creates ranked LLM-admission and tool-dispatch plans using remaining critical-path estimates and cross-resource externalities. An impact-triggered controller repairs the uncommitted plan when observed execution diverges from predictions. Evaluation replays a fixed batch of 192 recorded agent trajectories across resource configurations. The reported average speedup over veRL is 1.09x across the plotted configurations and 1.12x after excluding the severely tool-constrained T=2 configurations; a constructed deviation case shows a further 4.26% makespan reduction from runtime repair.
Critical strengths
-
The paper identifies a useful systems issue: trajectory priority depends on both LLM batching and downstream tool capacity. The examples in Section 2.3 make the mechanism concrete, and the plan-transfer experiment in Section 5.2.1 provides empirical support beyond the examples: target-specific plans outperform transferred plans, with little benefit when a serialized tool bottleneck removes scheduling flexibility. This helps explain when scheduling changes can matter.
-
The interface and evaluation include practical considerations. STARS changes admission order without changing the learning algorithm or execution engines, and identical replayed trajectories control for workload differences between schedulers. The paper reports absolute makespans, occupancy, weak-benefit configurations, and planning/repair overheads rather than speedup alone (Appendices B-C). These details make the observed efficiency improvement useful to systems practitioners.
Critical weaknesses
-
The experiments do not establish the incremental value of the main scheduling mechanism over prediction-based priority scheduling. Section 5.1 compares only against veRL's readiness/FIFO behavior. There is no baseline using the same predictions with remaining-critical-path priority alone, nor an ablation of the LLM/tool externality terms in Section 4.1. The platform-transfer experiment supports configuration dependence, but does not resolve whether the proposed counterfactual scoring is necessary for the reported gains. This leaves the central advance over the prediction-based schedulers motivating the paper insufficiently demonstrated.
-
Evidence for robust runtime adaptation is substantially narrower than the framework's scope. Appendix A uses one fixed replay batch; Section 5.3 changes one trajectory's suffix and reports repair benefit for one condition. Table 6 covers twelve conditions, but reports repair activity and overhead rather than improvements in repair-versus-frozen makespan. The paper also does not quantify prediction errors or simulator fidelity against live execution, both of which directly determine whether proposed repairs help. Replay is a useful controlled comparison, but the present evidence does not establish reliable benefits under representative prediction errors. These two gaps motivate a weak-reject recommendation on the current evidence.
Questions for authors
-
With identical forecasts and resource constraints, how does STARS compare with a remaining-critical-path-only scheduler? Can the existing experiments isolate the contribution of the LLM and tool externality terms, and specify the scoring weights and lookahead horizon used?
-
In the replay experiments, are composition-dependent LLM latencies measured by executing on the backend or produced by the profiled simulator? What held-out validation measures the simulator's error and the historical estimator's error without access to final replay outcomes?
-
What are the net repair-versus-frozen makespan changes for all twelve Table 6 conditions, and which trigger/acceptance thresholds were used? Do naturally occurring prediction errors show the same benefit as the constructed suffix-extension case? These clarifications would directly affect the assessment of the adaptive component.
We thank the reviewer. Repair is a recovery path, not a source of the reported gains — every headline number comes from the initial plan alone, and repair is evaluated separately (Section 5.3).
Q1: CP-only comparison, externality ablation, and score parameters
Event-CP is the remaining-critical-path-only scheduler: same forecasts, same resources, priority by remaining critical path, no candidate-branch counterfactual. At T=4 STARS wins against it in all eight capacities of the simulated sweep (4–64 accelerators), at 1.0717× mean speedup and a 6.54% mean makespan reduction; at (L=4, T=4) the reduction is 5.42%.
Section 4.1 makes all three corrections one-sided: the LLM batch externality sums only positive step-latency increases, tool wait is clipped at zero, and tool externality sums only positive increases in other tool phases' completion times. Each term is identically zero when its state is absent, so each acts in the regime its definition selects. In the 72-run, 27-contrast same-policy study, tool externality is positive in all nine backgrounds (mean 7.48%, median 6.83%), while removing all three corrections — keeping only R(c) — is materially worse: the gain is carried by the tool-externality term. H=8 token steps and three unit weights, fixed across cells.
Q2: Source of LLM latencies and held-out errors
Composition-dependent latencies come from the profile-driven simulator, but nothing it consumes is synthetic: the profile is measured on the target backend and engine, and every token count, tool service time, and dependency in the traces is recorded from real executions on that hardware (Section 5.1). The simulator supplies only their interleaving. The step costs are measured, not fitted — a new accelerator changes the table, not a parameter; only composition is learned. On the 53 requests held out by request ID (111 used for fitting), that model's residual is 18.42% MAPE on request service time, after measured engine queueing is removed.
The historical estimator gets the totals close — on the natural-history batches its predicted decode tokens and tool service land within about 5% and 20% of realized values — but it cannot place that mass per request: per-request error runs in the tens of percent, and above 100% for tool service. A plan built on absolute durations would inherit that spread.
The estimator is tested without access to outcomes: each forecast uses only histories completed before the common cutoff plus the public first-prompt token count.
The planner commits to ranks, not timings (Section 3.3); every arm shares one profile, so the model must respond correctly to composition and the residual error must be common. Section 5.2.1 tests exactly that: a plan built for one configuration loses 6.03% on average and up to 14.2% when transferred, and the advantage disappears at C=(4,1), where a single executor serializes the pool.
The evidence rests on one fixed batch, but not a single workload family: it mixes DevOpsGym, SWE-bench Verified, Terminal-Bench 2.1, and Terminal-Bench Pro.
Q3: Twelve repair conditions, thresholds, and natural errors
The twelve constructed conditions stress-test turning a forecast break into a shorter suffix; positive values mean repair shortens the rollout:
Protocol: 25% deviation threshold, 120 s coalescing and cooldown, 1 s gain margin, 60 s per-attempt control budget, 64 global attempts, two structural retries, two insertion overrides, fees frozen after calibration. The gradient is the mechanism: repair helps only when the frozen plan leaves room for a different order.
The held-out residual is a timing error, not a ranking error: the model is deliberately flat where the decision cannot matter, and the zero-error rows return exactly 0.00%. Natural-error benefit appears only where a batch contains a recoverable tail, so we report it as an operating envelope rather than a deployment promise. The revision will state the planning–repair separation explicitly in Section 5.1.