Accelerating Detailed Routing Convergence through Offline Reinforcement Learning

Afsara Khan; Austin Rovinski

REVIEW 5 major objections 6 minor 30 references

Accelerating Detailed Routing Convergence through Offline Reinforcement Learning

T0 review · 5 major / 6 minor · reviewed 2026-08-03 · deepseek-v4-flash

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Pith's one-line read This paper claims that an offline reinforcement-learning agent can pick per-iteration routing cost weights so that an iterative detailed router converges in fewer iterations—5% fewer on average and up to 31% fewer on unseen circuits—transla

desk verdict A real and useful new application of offline RL to detailed routing, with a clean held-out speedup — but the missing ispd19_test5 row has to be explained before the headline numbers can be trusted. read the letter →

arxiv 2512.03594 v2 pith:I64WRTGV submitted 2025-12-03 cs.AR

Afsara Khan , Austin Rovinski This is my paper

classification cs.AR

keywords detailedroutingofflinereinforcementlearningconservativeQ-learningcostweightschedulingdesignruleviolationsrip-upandreroutephysicalconvergenceacceleration

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

Every modern detailed router cleans up design-rule violations (DRVs) by repeatedly ripping up and rerouting nets, and each pass assigns costs to violations that push the search away from them. The authors' claim is that the static, hand-tuned schedules used for those costs are leaving speed on the table, and that an offline reinforcement-learning agent can choose the next iteration's cost weights from a compact summary of the design state. Trained on thousands of perturbation-sampled routing sequences, a conservative Q-learning policy converged on held-out test circuits in 5% fewer iterations on average and up to 31% fewer, which translated into 1.56x average and up to 3.01x faster runtime than the baseline router while keeping or improving final DRV counts. The learned weight paths look unlike the expert-curated baseline, and the gains appear on technology nodes never seen during training. If the claim holds, detailed routing speedup becomes a co-learnable control problem that can wrap any violation-costing router.

What carries the argument

Per-iteration dynamic selection of the router's four cost weights, driven by a conservative Q-learning (CQL) agent trained offline on perturbation-sampled trajectories; the agent maps a compact state—per-partition and total DRV counts, maximum and neighbor DRVs, wirelength, current weights, and design-level statistics—to the next weight vector, with reward combining DRV improvement, iteration penalty, convergence bonus, and a stuck penalty.

What would settle it

Build two test designs with identical aggregate state (same per-partition and total DRV counts, wirelength, weights, design stats) but different spatial layouts of violations; run the learned policy on both. If convergence iterations or final DRVs diverge materially, the state abstraction is incomplete and the transfer claim weakens.

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Extended reading notes

Core claim

The claim, stated in the authors' terms, is that an offline conservative Q-learning policy can replace the static or iteration-indexed cost-weight schedule of a detailed router and reliably drive faster convergence. Trained on perturbation-sampled sequences from 17 designs, the policy decides, at the end of each rip-up-and-reroute iteration, the next values of four cost weights (DRV cost, marker cost, fixed-shape cost, marker decay) from a state of aggregate DRV and wirelength statistics. On ten test circuits excluded from training, the policy used 5% fewer iterations on average and up to 31% fewer, speeding total runtime by 1.56x on average and up to 3.01x; final DRV counts were never worse

Load-bearing premise

The policy's decisions assume that the complete effect of a chosen weight vector on future convergence is captured by aggregate state—per-partition DRV counts, total DRVs, wirelength, current weights, and design statistics—so two designs with the same aggregate profile will respond identically to the same weights; exact violation locations are treated as irrelevant.

Editorial extensions

If this is right

A router's static cost weights are suboptimal: adopting a per-iteration learned weight policy yields 1.56x average and up to 3.01x runtime speedup on held-out circuits with equal or better DRV counts.
The approach is router-agnostic in the sense that it wraps the existing rip-up-and-reroute loop; any router that assigns costs to violations can host the same agent.
The policy generalizes across technology nodes, so a weight model trained on older designs can give speedups when first deployed on a newer technology.
Because the per-run inference cost is about 2 seconds, the speedup is most reliable on designs that take many iterations; already-fast designs may see slowdowns from overhead.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

The state excludes exact DRV locations by design; the authors' success suggests aggregate congestion features may be sufficient on these benchmarks, but a spatial-feature variant is the natural next experiment.
The 2s inference overhead explains the small design slowdowns; a practical deployment could gate the learned policy to designs whose baseline runtime exceeds a threshold.
The learned weight paths differ from the best seen in training data, hinting that many weight trajectories lead to equivalent convergence; this could be exploited to co-optimize wirelength or other objectives.
Reward omitted wirelength, matching the small (<1%) wirelength penalty; including a wirelength term in the reward would test the trade-off between convergence speed and route quality.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

Short version: this is a solid, useful paper with a real hole in the evidence table. The idea — using CQL to pick per-iteration cost weights in OpenROAD's detailed router — is a legitimate new application. Prior work used static or iteration-only schedules (Dr. CU, TritonRoute/OpenROAD) or online RL for custom circuits (Chen et al.), so the work fills a clear gap. The ISPD19 held-out evaluation is clean: those benchmarks were excluded from training, so the speedup is out-of-sample, not a refit. The integration is real: they measure with inference overhead included, and the 1.56x average / 3.01x peak on the reported rows is large. The weight analysis (Figs. 2, 7) is a nice addition, showing the learned policy does not just copy the best training sequences.

The main problem: Table III lists only 9 of the 10 ISPD19 test cases. ispd19_test5 is missing, and the abstract says 'all cases.' That matters here because the per-design runtimes swing from -6.98% to +66.84%; leaving out one case could move the 1.56x average considerably. The paper needs to report test5 or explain why it is absent. If it was omitted because the RL policy was slower or failed to converge, that qualifies the headline claim. The stress-test note is right: this is an internal inconsistency, not a trivial formatting slip.

A few smaller things. Runtimes are averaged over 10 runs but there are no error bars; on the slow, high-impact designs (test4, test10, bp_be) the differences are large enough that noise is unlikely to flip the conclusion, but the practice is worth fixing. The reward function is described as 'DRV Improvement Bonus,' 'Iteration Penalty,' etc., with no quantitative definition, so the result cannot be reproduced from the paper alone. The cross-technology claim rests on 'ISPD19 is a node the model had not seen,' but nothing in the text documents the training and test nodes. State sufficiency (aggregate DRV counts, no spatial coordinates) is an untested assumption; it might be fine, but it is the kind of thing a capacity experiment would illuminate. The paper says it aims to open-source code; as of v1 there is no artifact, so the empirical claim rests on the tables.

The central result is likely real — a clean held-out speedup, and even ignoring the missing row, the observed effects are large and directionally consistent on the high-cost designs. It deserves a serious referee. I would send it to peer review with a request for major revision: all 10 test cases, error bars, a quantitative reward definition, and code/data if the open-source statement is to hold.

Referee Report

5 major / 6 minor

Summary. This paper proposes using offline reinforcement learning (conservative Q-learning, CQL) to dynamically select per-iteration cost weights (DRC cost, marker cost, fixed-shape cost, marker decay) inside the OpenROAD detailed router. The authors generate training data by perturbing baseline weight schedules across 17 designs from the OpenROAD Design Suite and ISPD18, then train a CQL policy to choose weights that minimize the number of rip-up-and-reroute iterations until zero DRV convergence. They evaluate on nine reported ISPD19 benchmarks held out during training, claiming an average 1.56x runtime speedup (up to 3.01x) and equal or better DRV counts in all reported cases, along with signs of cross-technology generalization.

Significance. If the result holds, the paper offers a practical and relatively simple way to accelerate a state-of-the-art open-source detailed router by replacing a static weight schedule with a learned dynamic one, and it does so with a clean held-out evaluation protocol: ISPD19 is excluded from training. The use of an offline RL method (CQL) with perturbation-based data generation is a sensible fit for the expensive router environment. The authors also commit to open-sourcing code, which would materially strengthen reproducibility. However, the strength of the claim depends on the completeness and statistical rigor of Tables II-III, and several load-bearing details (exact reward specification, technology-node identities, and state-sufficiency justification) are not provided in the manuscript.

major comments (5)

[Table III / Section V.C] Table III reports only nine of the ten ISPD19 test benchmarks: ispd19_test5 is absent with no explanation, while the abstract claims 'maintaining or improving the DRV count in all cases' and Section V.A says ten unseen ISPD19 benchmarks were used. Since per-design runtime differences range from -6.98% to +66.84%, omitting test5 could materially change the average speedup and the 'all cases' DRV guarantee. Please add the missing row, explain any exclusion, and recompute totals and headline claims including test5.
[Section IV.B] The reward function is described only qualitatively ('DRV Improvement Bonus', 'Iteration Penalty', 'Convergence Bonus', 'Stuck Penalty' with importance labels). No formulas, coefficients, or reward scales are given, despite Section IV.B stating the reward was clipped and normalized with tanh. Because the headline metric (fewer iterations) is the training objective, the exact reward specification is essential for reproducibility and for assessing whether the reward balances convergence speed against DRV quality. Please provide the full quantitative reward definition.
[Section IV.B] The state representation deliberately excludes fine-grained spatial coordinates of DRVs, retaining only aggregate per-partition DRV counts, totals, wirelength, and current weights. The cross-design transfer claim assumes these aggregates are sufficient to determine which weight vector minimizes future iterations. This is not tested: two designs with identical aggregate state may respond differently to the same weights if local congestion structure matters. Please provide an ablation or feature-importance analysis, or a concrete experiment that varies the state granularity, to justify this assumption.
[Section V.A / Abstract / Section VI] The claim that learning generalizes across technologies is load-bearing for the abstract and conclusion, but no technology node is identified for the ISPD19 benchmarks or for the training designs. The only stated basis is that 'ISPD19 is in a technology node that the model had not seen before' (Section VI). Please specify the technology nodes of both training and test sets, and state whether any design-rule differences beyond node identity (e.g., routing layers, pitch, minimum-area rules) are relevant to the claimed transfer.
[Section V.A / Table III] Runtime and iteration results are said to be averaged over 10 runs, but no variance, standard deviation, or confidence intervals are reported. On designs where the observed difference is small (e.g., ispd19_test3: +1.89%, ispd19_test8: +0.66%, ispd19_test7: -0.63%), run-to-run noise could change the sign. Please report per-design statistics (mean plus spread) and, where meaningful, a paired test to support the per-design conclusions.

minor comments (6)

[Throughout] Typos: 'Dijkstra' is misspelled as 'Djiksta' in Section II.A; 'enchancements' should be 'enhancements' in Section II.A. Also, the IEEE reference for OpenROAD [5] is a GOMATECH paper, which may not be the standard citation; consider using the DAC/ICCAD version.
[Section V.A] The manuscript says 'across 29 standard and benchmark circuits' but Table II has 10 seen and Table III has 9 reported unseen rows, totaling 19; the count discrepancy needs clarification.
[Table II] The column 'Min.' is used for the fastest converging sequence in the training data but is not defined in the table caption or text; please define it explicitly and clarify how it was chosen.
[Section V.C / Figure 5] Figure 5 plots DRV convergence for the OpenROAD Design Suite, but the y-axis is log-scale and labels are partially garbled in the text extraction; ensure the figure is legible and axis labels are explicit.
[Section IV.A / Equation (1)] The CQL objective is written in a nonstandard form with a 'log-sum-exp' term; please verify the notation matches the cited reference [9] and define all symbols (e.g., \hat{B}^\pi, the Bellman operator) explicitly.
[Section III] The static design characteristics list includes 'number of routing layers' but it is not shown how these are incorporated into the state representation in Section IV.B; clarify their role.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: held-out ISPD19 evaluation is an independent out-of-sample test; reward alignment is a stated optimization, not a hidden circular prediction.

full rationale

The paper's central claim is an empirical speedup on ISPD19 benchmarks that were explicitly excluded from training. Section III states 'ISPD19 circuits were excluded from training data to be used as test data,' and Section V.A confirms '10 being unseen test benchmarks from ISPD19.' The RL policy selects routing cost weights to minimize iterations, and the headline metric is iteration count/runtime on those unseen benchmarks. This is a clean out-of-sample evaluation: the training data comes from OpenROAD Design Suite and ISPD18 designs, not from the test set. The reward function includes iteration penalty and convergence bonus, so the optimization target matches the evaluation metric, but that is not circularity — it is the defined goal of the method. No parameter is fitted to the ISPD19 results and then reported as a prediction. Self-citations to OpenROAD and TritonRoute are used to describe the baseline router, not to justify the learned policy's effectiveness. The absence of ispd19_test5 from Table III and the lack of variance bars are completeness/robustness concerns, but they do not make the derivation circular. Therefore, no circular step can be exhibited.

Assumptions & free parameters 9 free parameters · 5 assumptions · 0 invented entities

The central claim rests on a modest set of modeling assumptions: aggregate state sufficiency, a hand-designed reward proxy, perturbation coverage, determinism, and CQL's off-policy guarantees. The main free parameters are CQL hyperparameters and reward/perturbation design choices, partially reported in Table I or described qualitatively.

free parameters (9)

actor learning rate = 1.0e-3
CQL hyperparameter from Table I, tuned on training data.
critic learning rate = 4.0e-3
CQL hyperparameter from Table I, tuned on training data.
conservative weight (alpha) = 8.0e-1
CQL regularization coefficient from Table I, tuned on training data.
batch size = 128
CQL hyperparameter from Table I, tuned on training data.
initial temperature = 1.43298e-1
CQL hyperparameter from Table I, tuned on training data.
tau (Polyak) = 1.97555e-3
CQL hyperparameter from Table I, tuned on training data.
reward component weights
Section IV.B gives only 'order of importance' (DRV improvement, iteration penalty, convergence bonus, stuck penalty); exact weights are not specified but were chosen by hand.
perturbation mix ratio = ~60% perturbation / 40% Sobol random
Section III: the dataset split between perturbation-based sampling and Sobol random sampling is a design choice.
early stopping thresholds = critic loss 100x; action diff > 1.0
Section IV.C: thresholds chosen by hand to prevent policy collapse.

assumptions (5)

domain assumption The next-iteration optimal routing weights depend only on the aggregate state vector; exact violation coordinates are unnecessary.
Section IV.B: 'We deliberately exclude fine-grained spatial coordinates of violations to keep the state representation simple and generalizable.'
domain assumption A hand-designed reward (DRV improvement, iteration penalty, convergence bonus, stuck penalty) is a valid proxy for wall-clock convergence time and final solution quality.
Section IV.B defines the reward but gives no quantitative formula or validation that this reward correlates with runtime beyond the reported tables.
domain assumption Perturbation sampling around baseline weights plus Sobol random sampling on 17 training designs covers the weight/design distribution needed for unseen ISPD19 designs.
Section III generates 5,782 runs on OpenROAD Design Suite and ISPD18 designs; the transfer to ISPD19 relies on this coverage.
domain assumption OpenROAD's routing behavior is deterministic enough that a sequence of weight vectors determines the convergence trajectory, so policy evaluation on 10-run averages is meaningful.
Section V.A averages runtimes over 10 runs but does not report variances or random seeds, implying deterministic or near-deterministic behavior.
standard math CQL's conservative regularization controls out-of-distribution Q-values as claimed in Kumar et al. [9].
Section IV.A relies on the CQL objective (Eq. 1) and its theoretical properties for offline RL.

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Cite this review

Pith. "Pith review of Accelerating Detailed Routing Convergence through Offline Reinforcement Learning." pith.science (2026). https://pith.science/paper/I64WRTGV

@misc{pith2026251203594,
  author       = {Pith},
  title        = {Pith review of: Accelerating Detailed Routing Convergence through Offline Reinforcement Learning},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/I64WRTGV}},
  note         = {Machine review of arXiv:2512.03594}
}

read the original abstract

Detailed routing remains one of the most complex and time-consuming steps in modern physical design due to the challenges posed by shrinking feature sizes and stricter design rules. Prior detailed routers achieve state-of-the-art results by leveraging iterative pathfinding algorithms to route each net. However, runtimes are a major issue in detailed routers, as converging to a solution with zero design rule violations (DRVs) can be prohibitively expensive. In this paper, we propose leveraging reinforcement learning (RL) to enable rapid convergence in detailed routing by learning from previous designs. We make the key observation that prior detailed routers statically schedule the cost weights used in their routing algorithms, meaning they do not change in response to the design or technology. By training a conservative Q-learning (CQL) model to dynamically select the routing cost weights which minimize the number of algorithm iterations, we find that our work completes the ISPD19 benchmarks with 1.56x average and up to 3.01x faster runtime than the baseline router while maintaining or improving the DRV count in all cases. We also find that this learning shows signs of generalization across technologies, meaning that learning designs in one technology can translate to improved outcomes in other technologies.

Figures

Figures reproduced from arXiv: 2512.03594 by the authors.

**Figure 3.** Training and inference flow for conservative Q-Learning model [PITH_FULL_IMAGE:figures/full_fig_p004_3.png] view at source ↗

**Figure 4.** CQL Training Progress 0 1 2 3 4 5 10 1 10 0 10 1 10 2 10 3 10 4 aes 0 1 2 3 4 5 10 1 10 0 10 1 10 2 10 3 10 4 10 5 ariane136 0 2 4 6 8 10 12 14 10 1 10 0 10 1 10 2 10 3 10 4 10 5 bp_be 0 2 4 6 8 10 12 10 1 10 0 10 1 10 2 10 3 10 4 10 5 bp_fe 0 2 4 6 8 10 10 1 10 0 10 1 10 2 10 3 10 4 10 5 bp_multi 0 1 2 3 10 1 10 0 10 1 10 2 10 3 gcd 0 1 2 3 4 10 1 10 0 10 1 10 2 10 3 10 4 ibex 0 1 2 3 4 10 1 10 0 10 1 10 2 10 3 10 … view at source ↗

Figures from the paper (3 more)

**Figure 5.** Figure 5: DRV convergence comparison for the OpenROAD Design Suite [PITH_FULL_IMAGE:figures/full_fig_p005_5.png]

**Figure 6.** Figure 6: Baseline weight configuration for all designs. Truncated after iteration [PITH_FULL_IMAGE:figures/full_fig_p006_6.png]

**Figure 7.** Figure 7: Weight selections by our RL model vs. weights used in the fastest [PITH_FULL_IMAGE:figures/full_fig_p006_7.png]

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Reference graph

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Pith tools

Reviewed August 3, 2026 · model on record in the stance chip above.

[1] [1]

An algorithm for path connections and its applications,

C. Y . Lee, “An algorithm for path connections and its applications,”IRE Transactions on Electronic Computers, vol. EC-10, no. 3, pp. 346–365, 1961

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