acceptodds
Under review as a conference paper at ICLR 2027

CARVE: Breaking Data Barriers in Chip Placement by Harnessing Reusable Expertise

Abstract

Pretrained macro-placement policies can reduce repeated optimization across circuits, but deployment often exposes them to unfamiliar designs when the original training data are unavailable. Repeatedly fine-tuning a single serving model can overwrite earlier improvements, while simply saving checkpoints does not determine where they can be reliably reused. We introduce Continual Adaptation through the Reuse of Validated Expertise (CARVE), a framework that represents accumulated expertise as a frozen base policy, immutable specialists, and task-specific credentials obtained through local validation. For a new task, CARVE first checks existing specialists and trains a new specialist from the frozen base only when none qualifies. Under fixed task distributions and validation rules that control cumulative error, we establish expected-performance guarantees for repeated reuse. For bounded losses, we also derive matching worst-case bounds on the local samples needed for reliable reuse. In macro placement, a reuse-first follow-up reduces recorded training time by 58.5% (9.66 to 4.01 hours), while mean HPWL gain changes only from 8.41% to 7.86%. In a simulated receiving deployment, imported specialists are reused on six of seven new IBM circuits with no receiver-side training, achieving a 5.76% mean HPWL gain. Navigation studies provide complementary evidence on repair retention and repeated adaptation.

Primary area:
infrastructure, software libraries, hardware, systems, etc.
Keywords:
Electronic design automation, Chip macro placement, Continual adaptation

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_wu64OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
Paper summary

CARVE proposes a continual adaptation framework for pretrained policies when the provider’s training data are unavailable. It retains a frozen base model and immutable specialists, using local validation to authorize each specialist for specific tasks. The proposed reuse-first workflow checks existing specialists before training a new model from the base. The paper provides conditional expected-performance guarantees and sample-complexity bounds for reliable reuse. Experiments in crowd navigation and chip macro placement examine retention, cross-task reuse, and simulated transfer between operators.

Critical strengths

A clear protocol for retaining and reusing adaptations. The framework explicitly separates preserving a trained model from authorizing its use on a particular task. The reuse-first and receiving-operator experiments provide concrete examples of reusing existing specialists without source training data, with reduced new training in the recorded settings.

Critical weaknesses

The placement evaluation does not establish gains in complete, legal layouts. Appendix F states that IBM scoring is limited to the placed subset and that the evaluator performs no final overlap or boundary checks. Consequently, the reported HPWL improvements do not establish better complete, legal placements. This substantially limits the evidence for the main application.

The additional benefit over simple model caching is modest in the main revisit experiment. Cache-only achieves a 7.04% mean HPWL gain with 10.53 hours of repair work, compared with 8.41% and 10.36 hours for CARVE. Although the paper includes diagnostic analyses, the evidence does not convincingly establish how much the admission mechanism adds beyond saving and retrieving task-specific models.

The quality–cost benefit of reuse-first is not sufficiently isolated. Across the ten revisits to the five reused circuits, mean HPWL gain is 11.91% with reuse, compared with 17.33% with target-specific training. Training seeds and integration code also differ between the executions. These differences make it difficult to attribute the aggregate quality and cost changes specifically to the reuse-first rule.

Questions for authors
  1. How do the main HPWL improvements change when evaluation covers all macros and includes final overlap and boundary checks? Please report the proportion of complete, valid placements alongside their placement quality.

  2. When the trained candidates and evaluation cases are held fixed, how much does admission improve subsequent placement quality and reduce regressions relative to Cache-only? This would help establish the contribution of validation beyond model retention.

  3. Can a comparison using identical integration code and matched training seeds confirm the reported quality–repair-cost trade-off? For this controlled comparison, please distinguish outcomes on reused circuits from gains due to newly trained specialists.

8 comments
AuthorsOpenReview ↗

Reply to Reviewer wu64 (Part 1 of 3)

Thank you for the careful review. We address placement validity, admission beyond caching, and the controlled quality–cost comparison below.

1. Complete and legal placements (Weakness 1)

W1-1: The placement evaluation does not establish gains in complete, legal layouts. Appendix F states that IBM scoring is limited to the placed subset and that the evaluator performs no final overlap or boundary checks.

Thank you for the comment. ChiPFormer's policy places 256 modules per IBM circuit (ChiPFormer paper, App. A.1 and Table 5). Our census counts modules taller than the 16-unit standard cells and finds 285–786 macros per IBM circuit.

Every method now uses the same procedure. Completion places the missing macros greedily on the policy's grid without moving policy-placed macros. We then legalize each layout and score every net that ChiPFormer retains for macro placement. A separate geometry checker verifies every final layout.

W1-2: Consequently, the reported HPWL improvements do not establish better complete, legal placements. This substantially limits the evidence for the main application.

We note that the relevant results are given below. The gains persist on complete, legal layouts, and the ranking is unchanged (Table R1). CARVE beats the base on 12 of 18 requests, ties on 6, and loses none. The ties are each circuit's first request, which CARVE serves with the base.

Gains are relative to the frozen base, the released ChiPFormer checkpoint. Table R1 reports all four methods under both scorers.

Table R1. Mean HPWL gain over the frozen base, averaged over the requests shown. 

MethodAll 18 requestsOnly the 12 revisits
CARVE (Ours)9.78% (11.22%)14.68% (16.83%)
Cache-only7.24% (7.91%)10.86% (11.86%)
RS1.18% (1.16%)−0.33% (−0.14%)
Overwrite−4.57% (−4.40%)−8.16% (−8.04%)

 

2. Admission beyond model caching (Weakness 2)

W2-1: The additional benefit over simple model caching is modest in the main revisit experiment. Cache-only achieves a 7.04% mean HPWL gain with 10.53 hours of repair work, compared with 8.41% and 10.36 hours for CARVE.

Thank you for this observation. Table R1 gives both methods on circuits under both scorers. On complete, legal layouts, CARVE reaches a 9.78% mean gain with 7.60 h of repair, and Cache-only 7.24% with 7.86 h.

W2-2: Although the paper includes diagnostic analyses, the evidence does not convincingly establish how much the admission mechanism adds beyond saving and retrieving task-specific models.

We note the following distinction. The totals above compare different trained specialists. To measure admission alone, we hold Cache-only's specialists and evaluation trials fixed and add only the test (Q2). Admission then raises the mean revisit gain by 0.90 points and removes every revisit worse than the base (from 2 to 0).

AuthorsOpenReview ↗

Reply to Reviewer wu64 (Part 2 of 3)

3. Controlled comparison of train-each and reuse-first (Weakness 3)

W3: The quality–cost benefit of reuse-first is not sufficiently isolated. Across the ten revisits to the five reused circuits, mean HPWL gain is 11.91% with reuse, compared with 17.33% with target-specific training. Training seeds and integration code also differ between the executions. These differences make it difficult to attribute the aggregate quality and cost changes specifically to the reuse-first rule.

Thank you for highlighting this concern. The circuit replay uses identical code, specialist files and evaluation seeds for both rules, so only the rule differs. It trains no new models; training times come from E2's records.

We apply both rules to each of three specialist sets: A from CARVE's E2 training, B from Cache-only's, and C from RS's. All specialists used the same trainer and budget and started from the frozen base, with different training seeds across sets. A set is only a pool of specialists, not a method. Reuse-first keeps E2-X's Holm correction and selection rule.

Table R2. Mean gain over the 18 requests on circuits, after completion and legalization..

Specialist setMean gain: train-eachMean gain: reuse-firstTrain-each minus reuse-first (points)Recorded training time saved
A9.78%7.33%2.4542.7%
B7.84%7.18%0.6661.8%
C6.64%5.12%1.5242.6%

Including failed attempts, the training savings are 42.7%, 58.1% and 50.7% for A, B and C, respectively. Under the original scorer, train-each exceeds reuse-first by 4.20, 1.95 and 3.05 points, respectively.

Thank you for highlighting this trade-off. The controlled replay confirms this cost and shows where it comes from:

  • Both rules use the base for each circuit's first request, before any training or reuse decision.
  • When both rules train a circuit, the replay uses the identical specialist and admission decision. Their later results therefore match, including any fallback to the base.
  • Only revisits served by another circuit's specialist under reuse-first can differ. On those revisits, train-each uses the circuit's own specialist if admitted, or the base otherwise.

Table R3. Mean HPWL gain on the revisits that reuse-first serves with another circuit's specialist.

Specialist setCircuits using another circuit's specialistMean gain: train-eachMean gain: reuse-first
Aibm15, ibm13, bigblue116.75%9.39%
Bibm18, ibm15, bigblue1, ibm1012.33%10.85%
Cibm13, bigblue1, ibm1012.74%8.18%

All other requests have identical outcomes under both rules. Each gap in Table R2 is therefore the Table R3 difference spread over all 18 requests; for set A, (16.75 − 9.39) × 6 / 18 = 2.45 points.

AuthorsOpenReview ↗

Reply to Reviewer wu64 (Part 3 of 3)

4. Complete, valid placements and placement quality (Q1)

Q1-1: How do the main HPWL improvements change when evaluation covers all macros and includes final overlap and boundary checks?

Thank you for the question. On the same 18 requests, CARVE keeps the highest mean gain: 9.78% under the new evaluation and 11.22% under the original scorer. Table R1 gives all four methods; the ranking is unchanged.

Q1-2: Please report the proportion of complete, valid placements alongside their placement quality.

Thank you for this request. Before completion, only bigblue1's 450 trials contained every macro. No raw layout had a macro-macro or macro-fixed-object overlap, consistent with ChiPFormer's position mask (ChiPFormer paper, Sec. 3.3). However, 295 layouts contained at least one macro crossing the boundary: 162 on ibm07 and 133 on ibm15. Neither ChiPFormer nor MaskPlace addresses these crossings.

After completion and legalization, 2,700 of 2,700 layouts (100%) are complete and legal, as confirmed by a separate geometry checker. Per method, the share of complete, legal layouts rises from 90 of 540 (17%, all on bigblue1) to 540 of 540. Table R1 reports their quality.

5. Admission with fixed candidates and evaluation cases (Q2)

Q2: When the trained candidates and evaluation cases are held fixed, how much does admission improve subsequent placement quality and reduce regressions relative to Cache-only? This would help establish the contribution of validation beyond model retention.

Thank you for suggesting this comparison. We keep Cache-only's specialists and all evaluation trials fixed. Admission rejects only ibm18's specialist: its admission-test gain is −2.77%, with p = 0.956. Its revisits then use the base.

Mean gain over the 12 revisits rises from 10.86% to 11.75%, by 0.90 points before rounding. The number of revisits worse than the base falls from 2 to 0; the worse of the two had been −7.05%. Testing takes 8 minutes. We store 5 specialist files instead of 6 (−16.7%). Across the three specialist sets defined in Section 3 above, admission rejects 3 of 18 trained specialists. In these runs, the 15 admitted specialists beat the base on all 30 of their later revisits; over circuits, the 21 admitted specialists beat it on all 42.

6. Controlled quality–cost comparison and reused-circuit outcomes (Q3)

Q3-1: Can a comparison using identical integration code and matched training seeds confirm the reported quality–repair-cost trade-off?

Thank you for the question. The controlled replay confirms the trade-off and measures its size under a common implementation: across the three sets, reuse-first saves 43–62% of recorded training time (mean 49%) at a cost of 0.66–2.45 percentage points of mean HPWL gain (mean 1.54). This confirms the trade-off stated in Section 3.2 under a common implementation. With set A, repair time falls from 7.60 h to 4.19 h. Completion and legalization add under one minute, which these times do not include.

Q3-2: For this controlled comparison, please distinguish outcomes on reused circuits from gains due to newly trained specialists.

Thank you for requesting this distinction. Only the revisits in Table R3 can differ. Circuits that both rules train have identical outcomes.

Reviewer_QVG3OpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

This paper examines the study of chip macro placement. It introduces a framework known as CARVE, in which separate “specialists” are trained from a frozen base model. The intended use of the framework is an online procedure where when new requests come in, current specialists are evaluated, and if none are suitable then a new specialist is trained. In the fallback case the base model is used.

The assumption in the setting is that a new “request” contains a set of tasks, which presumably is used for training the new specialist (this was unclear).

Critical strengths

On evaluations, the proposed method appears outperform a simple baseline of overwriting the previous policy.

Critical weaknesses

There are several critical weaknesses in this paper: *First, the related work is insufficient and only cites a few works, most of which are general “learn without forgetting works” from before 2024. *The introduction and Section 2 are confusingly written and unclear. It is unclear what the proposed framework is describing, whether it is related to the setup of the setting or the novel contribution. The idea of learning a continual set of specialists is not new and there is no comparison to prior works. *The description of the tasks is overly complicated, and yet it is unclear what the actual training and evaluation procedure is.

Questions for authors

n/a

4 comments
AuthorsOpenReview ↗

Reply to Reviewer QVG3 (Part 1 of 3)

Thank you for the feedback. We address each concern with evidence and concrete revisions.

The assumption in the setting is that a new “request” contains a set of tasks, which presumably is used for training the new specialist (this was unclear).

Thank you for the comment. A request belongs to one task family. Section 2.1 states: “Each request may contain several trials or episodes, each called a case z,” and identifies each placement family with one circuit (p. 3, lines 149–151). An ibm07 request contains 30 placement trials, not 30 tasks.

Training is conditional. The introduction states: “If no examined specialist qualifies, CARVE trains a new candidate from the frozen base and accepts it only after it passes the same comparison,” followed by “Each request is served before the repair it triggers, so new specialists and credentials affect later requests” (p. 2, lines 98–100). Section 2.2 separately denotes training data by DftrD_f^{\mathrm{tr}}.

We will introduce Section 2 with this consolidated definition:

A family specifies a circuit or a navigation geometry and pedestrian model. A request is one family arrival; a case is one seeded trial or episode. CARVE serves with an approved specialist or the base. Eligible repair checks stored specialists before training on current-family data; passing evaluation authorizes later service.

W1: First, the related work is insufficient and only cites a few works, most of which are general “learn without forgetting works” from before 2024.

Thank you for raising this point. We respectfully disagree with this characterization of the discussion's scope, while welcoming suggestions for further relevant work. The submitted introduction and Section 4 cover:

DirectionReferences already citedRelation to CARVE
Model isolation and modular learningProgressive Neural Networks [1], PackNet [2], CompoNet (ICML 2024) [3]Preserve and combine prior capabilities; CompoNet is also a baseline.
Adaptation without source examplesLearning without Forgetting [4], Tent [5]Source-data restrictions do not exclude all adaptation methods.
Continued trainabilityDohare et al. (Nature 2024) [6], Lyle et al. [7, 8]Plasticity loss and interventions that preserve trainability.
Validation and placementHigh Confidence Policy Improvement [9], ChiPFormer [10], Lee et al. (ICML 2025) [11]Validation precedent, placement trainer, and recent placement context.

These references already appear in the submission, including Lee et al.'s Chip Placement with Diffusion Models (ICML 2025). We do not claim that most references are recent.

We will consolidate these connections and add Expert Gate [12] and Arrow [13]. Expert Gate uses autoencoders for expert selection and task relatedness; Arrow selects LoRA adapters without retraining. CARVE compares current-family performance against the base to authorize reuse and decide whether to train. The request supplies its family. Section 4 recognizes that source-data restrictions do not exclude all adaptation methods (lines 467–469); LwF preserves earlier predictions using current-task inputs.

If there is a particular recent paper we have missed, please feel free to share it in a follow-up. We would be happy to review it and incorporate the relevant connections into our discussion.

AuthorsOpenReview ↗

Reply to Reviewer QVG3 (Part 2 of 3)

W2: The introduction and Section 2 are confusingly written and unclear. It is unclear what the proposed framework is describing, whether it is related to the setup of the setting or the novel contribution. The idea of learning a continual set of specialists is not new and there is no comparison to prior works.

We note that the distinction is as follows. The setting provides a pretrained policy, recurring tasks, and local feedback without provider examples. CARVE's contribution is the protocol and analysis: preserve models, record model–family permissions, check reuse before training, and fall back to the base, using the existing domain trainer.

An ibm07 specialist remains available after adapting to ibm18, but storage alone does not establish suitability for ibm13. Passing an ibm13 comparison authorizes unchanged reuse and can avoid training. We will distinguish preservation, suitability, and further training before the notation, and replace “We introduce a key concept called a specialist” with “We call a separately adapted copy of the pretrained policy a specialist.”

Thank you for raising this comparison. We respectfully disagree that there is no comparison to prior work. Section 3.1 and Table 2 compare with adapted CompoNet (ICML 2024) [3]. Table A12 describes its PPO-trained modules with a frozen base and prefix, without CARVE's admission rule. On the displayed navigation stream, CARVE achieves 59.8% success versus CompoNet's 54.4%, with repair times of 2.96 h versus 2.49 h. CARVE has higher success and higher cost; the same arrival order but separate case blocks do not establish paired statistical significance. If you had a different prior method or comparison in mind, please let us know; we would be happy to explain its relationship to CARVE and discuss what further comparison would be informative.

The additional placement experiments isolate the deployment decisions. Holding Cache-only's specialists and evaluation cases fixed, admission rejects only ibm18's specialist. Including the corrected adaptec2/adaptec3 reruns, mean HPWL gain over 16 revisits rises from 18.29% to 18.96%, and revisits worse than the base fall from two to zero. Separately, the controlled circuit comparison holds code, specialists, and evaluation seeds fixed between train-each and reuse-first. Across three specialist sets, reuse-first saves 31–47% of recorded training time for attempts that produced a specialist, at a cost of 0.50–1.84 percentage points of mean HPWL gain. This measures admission beyond caching and reuse's quality–cost trade-off.

Proposition 1 gives non-worse expected performance under repeated reuse with fixed models/distributions and cumulative validation-error control; only new approvals consume that budget. For bounded losses and fresh independent cases, Theorem 2 gives matching worst-case sample bounds, Θ(γ−2log⁡(J/δ))\Theta ({\gamma }^{-2}\log (J/\delta )), for a fixed library of JJ specialists. With probability at least 1−δ1-\delta, selection is non-worse than the base and chooses a specialist whenever one has population improvement at least γ\gamma. This threshold differs from the empirical admission margin; experimental gates do not directly instantiate this guarantee. We will foreground this contribution and its evidence.

AuthorsOpenReview ↗

Reply to Reviewer QVG3 (Part 3 of 3)

W3: The description of the tasks is overly complicated, and yet it is unclear what the actual training and evaluation procedure is.

Thank you for this suggestion. We will consolidate the details from Sections 2–3 and Appendices A.1, A.3, and A.6 before the notation:

ComponentChip macro placementCrowd navigation
Task and input/outputOne circuit's netlist, macro sizes, and constraints; output: macro locations.Family: geometry and pedestrian behavior. Request: scene size and crowd count. Observations map to robot actions.
Repair triggerEligible circuit without an approved specialist.Eligible family with at most 88 successes in 100 monitoring episodes.
TrainingFine-tune a frozen-base ChiPFormer copy [10] on current-circuit experience; 4,800 seconds per attempt, at most three attempts if no candidate is produced.Fine-tune a frozen-base SARL copy [14] on current-family simulations for 60,000 steps.
Admission30 paired trials; at least 5% lower median HPWL and one-sided paired Wilcoxon p<0.05p<0.05. Extension uses the specified Holm correction.100 paired episodes; at least 15 extra successes (15 percentage points).
Service evaluation30 matched trials/request. Gain: 100(1−m/m0)100(1-m/{m}_{0}) for method/base median HPWL; average request-level gains. Corrected evaluation consistently completes and legalizes layouts.100 episodes/request; success means reaching the goal within 90 seconds without swept-volume contact.

Each family receives at most one bounded training session per deployment run; rejection leaves it on the base. Training uses current-family data without provider examples or previous-family replay. New approvals affect only later service.

The main placement retention study trains each new circuit; subsequent extension checks do not avoid training or change routing. The follow-up and controlled replay test reuse-first (Section 2.1, lines 175–177; Section 3.2, lines 357–359). We will highlight this distinction. Navigation admission and service use different case blocks, but training/admission disjointness is not established by the original records; we retain this limitation.

The additional placement results are already in the appendix; the clarifications above will enter the main text. We hope these responses address the four concerns and would appreciate reconsideration. If a specific distinction or step remains unclear, please let us know; we would be glad to clarify it.

ref:

[1] Progressive Neural Networks, nips 2016

[2] PackNet: Adding Multiple Tasks to a Single Network by Iterative Pruning, cvpr 2018.

[3] Self-Composing Policies for Scalable Continual Reinforcement Learning, icml 2024.

[4] Learning without Forgetting, tpami 2018. 

[5] Tent: Fully Test-Time Adaptation by Entropy Minimization, iclr, 2021.

[6] Loss of plasticity in deep continual learning, Nature 2024.

[7] Understanding Plasticity in Neural Networks, icml 2023.

[8] Disentangling the Causes of Plasticity Loss in Neural Networks. Proceedings of the 3rd Conference on Lifelong Learning Agents, 2024.

[9] High Confidence Policy Improvement, icml 2015.

[10] ChiPFormer: Transferable Chip Placement via Offline Decision Transformer, icml 2023.

[11] Chip Placement with Diffusion Models, icml 2025.

[12] Expert Gate: Lifelong Learning With a Network of Experts, cvpr 2017.

[13] Towards Modular LLMs by Building and Reusing a Library of LoRAs, icml 2024.

[14] Crowd-Robot Interaction: Crowd-Aware Robot Navigation With Attention-Based Deep Reinforcement Learning, icra 2019.

Thank you again for your review. As the discussion period ends soon, we wanted to check whether our response and the revised manuscript address your comments. We would be glad to clarify anything further.

Thank you,

Authors

Reviewer_7KxNOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2(+1)
Read review
Paper summary

CARVE addresses adaptation of pretrained placement policies when source training data are unavailable. It stores an immutable base policy, frozen specialists, and task-specific validation credentials. Existing specialists are checked before new training, and new specialists start from the base. The paper gives repeated-reuse guarantees under fixed distributions and cumulative validation-error control, plus matching-order sample bounds for bounded losses. Navigation and macro-placement studies examine retention, cross-task reuse, and simulated transfer between operators. The placement reuse follow-up reports lower recorded training time with a quality trade-off.

Critical strengths
  1. Separating model preservation from authorization to serve a particular task is a useful deployment abstraction. It addresses an important distinction: retaining an adapted checkpoint does not establish that it is suitable for another circuit. This is consequential in source-data-restricted deployments.

  2. The statistical analysis makes its assumptions explicit and distinguishes expected improvement from per-instance performance. The matching-order validation bounds provide a useful characterization of the evidence needed for reuse (Proposition 1 and Theorem 2, p. 5; proofs, pp. 32–36). The appendices also preserve unfavorable results and disclose important limitations, making the empirical claims easier to assess.

Critical weaknesses
  1. The principal placement metric has not been validated on complete, legal placements. Appendix F explicitly states that IBM scoring remains limited to the placed subset, that the evaluator has no final overlap or boundary check, and that full-placement legality is unverified (p. 38). Consequently, lower HPWL does not yet establish better usable macro placement. A shared evaluator alone does not resolve whether omitted macros, inconsistent coverage, or illegal layouts affect the relative results. This is my primary reason for rejection: the main application requires evidence that the reported gains survive complete coverage and consistent legality checks.

  2. The main reuse comparison does not isolate the effect of checking specialists before training. E2 trains each new circuit, whereas E2-X changes both training seeds and integration code; some baseline attempts were also affected by a circuit-registration issue (p. 17; Appendix B.2, pp. 23–24). The authors explicitly report the quality trade-off: on ten revisits to the five reused circuits, mean HPWL gains are 17.33% with own-circuit training versus 11.91% with reuse, with lower gains for reuse on nine visits (p. 24; Table D6, p. 30). New adaptec2 training partly offsets this gap in the overall average. These observations support reuse as a descriptive cost–quality trade-off, but do not identify its causal benefit under a common implementation. I acknowledge that Appendix C already includes a matched-candidate navigation comparison (Table C1, p. 25) and a fixed-candidate placement-gate comparison (Table C5, p. 27); neither is the same-code train-each-circuit versus reuse-first experiment. The empirical gates are also explicitly distinguished from the theoretical guarantee on pp. 5 and 36, so I do not treat lack of retrospective certification as an undisclosed flaw or a counterexample to the theorem.

Questions for authors
  1. Are the scored macro and net sets identical across methods? Please report expected versus placed macro counts and overlap/boundary violations. Do the main gains persist after completing and consistently legalizing the placements?

  2. After correcting the registration issue, does a same-code, paired-seed comparison of train-each-circuit and reuse-first retain the claimed quality–cost advantage? Please distinguish the reused-circuit subgroup from gains due to newly trained adaptec2.

5 comments
AuthorsOpenReview ↗

Reply to Reviewer 7KxN (Part 1 of 3)

Thank you for the detailed review. We address the placement evaluation and the controlled reuse comparison below.

1. Complete and legal placements (Weakness 1)

W1-1: The principal placement metric has not been validated on complete, legal placements. Appendix F explicitly states that IBM scoring remains limited to the placed subset, that the evaluator has no final overlap or boundary check, and that full-placement legality is unverified (p. 38).

Thank you for the comment. All three are now checked. We reproduced the recorded HPWL exactly for all 2,700 service trials: 5 methods, including the base, × 18 requests × 30 seeds.

We then applied the same procedure to every method. Completion places the missing macros greedily on the policy's grid without moving policy-placed macros. Legalization follows. We score every net that ChiPFormer retains for macro placement: nets joining two or more macros or fixed objects, excluding standard cells. A separate geometry checker confirms that all 2,700 final layouts contain every macro, with no overlaps or boundary crossings.

W1-2: Consequently, lower HPWL does not yet establish better usable macro placement. A shared evaluator alone does not resolve whether omitted macros, inconsistent coverage, or illegal layouts affect the relative results. This is my primary reason for rejection: the main application requires evidence that the reported gains survive complete coverage and consistent legality checks.

We note that the relevant results are given below. After completion and legalization, CARVE beats the base on 12 requests, ties on 6, and loses none. The ties are the first requests for each circuit, which CARVE serves with the base. All methods use identical macro and net sets. Legalization alone changes any gain by at most 0.16 points. The method ranking is the same under both scorers, and CARVE beats Cache-only on 10 of the 12 revisits under both scorers.

Table R1 covers circuits and 18 requests.

Table R1. Mean HPWL gain over the frozen base, averaged over the requests shown.

MethodAll 18 requestsOnly the 12 revisits
CARVE (Ours)9.78% (11.22%)14.68% (16.83%)
Cache-only7.24% (7.91%)10.86% (11.86%)
RS1.18% (1.16%)−0.33% (−0.14%)
Overwrite−4.57% (−4.40%)−8.16% (−8.04%)

2. Controlled comparison of train-each and reuse-first (Weakness 2)

W2-1: The main reuse comparison does not isolate the effect of checking specialists before training. E2 trains each new circuit, whereas E2-X changes both training seeds and integration code; some baseline attempts were also affected by a circuit-registration issue (p. 17; Appendix B.2, pp. 23–24).

Thank you for highlighting this point. We now replay the train-each and reuse-first rules with identical code, specialists and evaluation seeds, so only the rule differs. This circuit replay trains no new models; it uses E2's specialists and training-time records.

We apply both rules to each of three specialist sets. A holds the specialists that CARVE trained in E2, B those that Cache-only trained, and C those that RS trained; all used the same trainer and budget, with different seeds. A set is only a pool of specialists, not a method. Reuse-first keeps E2-X's Holm correction and selection rule.

Table R2. Mean gain over the 18 requests on circuits

Specialist setMean gain: train-eachMean gain: reuse-firstTrain-each minus reuse-first (points)Recorded training time saved
A9.78%7.33%2.4542.7%
B7.84%7.18%0.6661.8%
C6.64%5.12%1.5242.6%

The training savings are 42.7%, 58.1% and 50.7% for A, B and C, respectively. Under the original scorer, train-each exceeds reuse-first by 4.20, 1.95 and 3.05 points, respectively.

AuthorsOpenReview ↗

Reply to Reviewer 7KxN (Part 2 of 3)

W2-2: The authors explicitly report the quality trade-off: on ten revisits to the five reused circuits, mean HPWL gains are 17.33% with own-circuit training versus 11.91% with reuse, with lower gains for reuse on nine visits (p. 24; Table D6, p. 30).

Thank you for highlighting this trade-off. The controlled replay confirms this cost and shows where it comes from:

  • Both rules use the base for each circuit's first request, before any training or reuse decision.
  • When both rules train a circuit, the replay uses the identical specialist and admission decision. Their later results therefore match, including any fallback to the base.
  • Only revisits served by another circuit's specialist under reuse-first can differ. On those revisits, train-each uses the circuit's own specialist if admitted, or the base otherwise.

Table R3. Mean HPWL gain on the revisits that reuse-first serves with another circuit's specialist.

Specialist setCircuits using another circuit's specialistMean gain: train-eachMean gain: reuse-first
Aibm15, ibm13, bigblue116.75%9.39%
Bibm18, ibm15, bigblue1, ibm1012.33%10.85%
Cibm13, bigblue1, ibm1012.74%8.18%

All other requests have identical outcomes under both rules. Each gap in Table R2 is therefore the Table R3 difference spread over all 18 requests; for set A, (16.75 − 9.39) × 6 / 18 = 2.45 points.

Reuse-first has lower gain on all revisits in A and in C. In B, it has higher gain on the revisits of ibm18 and ibm10.

W2-3: New adaptec2 training partly offsets this gap in the overall average.

Thank you for the comment. In our rerun, both rules train adaptec2 and adaptec3 and use identical specialists there. Their requests therefore add no difference between the rules and cannot offset the gap. Table R3 is unchanged; the rerun is reported below.

We reran both circuits under their own settings and trained one specialist per circuit for each set. All specialists passed admission: every p ≤ 0.0021 and every improvement ≥ 11.9%. Both rules train and use the same specialist on each circuit, and their requests add exactly zero difference between the rules.

Table R4. Gap between the rules over the 24 requests

Specialist setTrain-each minus reuse-first (points)Recorded training time saved
A1.84 (2.45)31.6% (42.7%)
B0.50 (0.66)46.9% (61.8%)
C1.14 (1.52)31.3% (42.6%)

For CARVE and Cache-only, the rerun trained new adaptec specialists. Over circuits, they average 14.91% and 12.19% across 24 requests; the original scorer gives 14.79% and 11.74%. Across 16 revisits, they average 22.37% and 18.29%; the original scorer gives 22.19% and 17.61%. CARVE has no revisit worse than the base. Cache-only has two, both on ibm18.

The rerun adds 1,290 trials, all complete.

W2-4: These observations support reuse as a descriptive cost–quality trade-off, but do not identify its causal benefit under a common implementation.

We note that the following comparison addresses this point. The controlled replay measures this trade-off under a common implementation. Reuse-first saves 43–62% of recorded training time, 49% on average, at a cost of 0.66–2.45 points of mean gain, 1.54 on average.

This confirms the trade-off stated in Section 3.2 under a common implementation.

W2-5: I acknowledge that Appendix C already includes a matched-candidate navigation comparison (Table C1, p. 25) and a fixed-candidate placement-gate comparison (Table C5, p. 27); neither is the same-code train-each-circuit versus reuse-first experiment.

We note the following clarification. Table R2 supplies that controlled rule comparison. Separately, we ran a test that complements Table C5: we hold Cache-only's specialists and all evaluation trials fixed and add only admission. Admission rejects ibm18's specialist. The mean gain over the 12 revisits rises from 10.86% to 11.75%, and revisits worse than the base fall from 2 to 0.

W2-6: The empirical gates are also explicitly distinguished from the theoretical guarantee on pp. 5 and 36, so I do not treat lack of retrospective certification as an undisclosed flaw or a counterexample to the theorem.

Thank you. We keep the empirical gates separate from the theorem's guarantee.

AuthorsOpenReview ↗

Reply to Reviewer 7KxN (Part 3 of 3)

3. Macro and net coverage, counts, and legality (Q1)

Q1-1: Are the scored macro and net sets identical across methods?

Thank you for the question. Yes. All 450 trials per circuit use identical macro and net sets: 5 methods × 3 requests × 30 seeds. We checked this by name, not just by count.

Q1-2: Please report expected versus placed macro counts and overlap/boundary violations.

Thank you for this request. Macro counts. ICCAD04 files do not label macros. ChiPFormer selects 256 modules as macros and treats the rest as standard cells (ChiPFormer paper, App. A.1 and Table 5). Our census counts every module taller than the 16-unit standard cells as a macro. It finds 291 macros in ibm07, 285 in ibm18, 393 in ibm15, 424 in ibm13, and 786 in ibm10. On each IBM circuit, every method's policy places 256 modules; completion places the remaining macros. On bigblue1, the policy places every macro.

Overlaps and boundary crossings. No raw layout has a macro-macro or macro-fixed-object overlap, consistent with ChiPFormer's position mask (ChiPFormer paper, Sec. 3.3 and App. A.4). Macros cross the canvas boundary in 162 of 450 ibm07 trials and 133 of 450 ibm15 trials, and nowhere else; neither ChiPFormer nor MaskPlace addresses such crossings. Per method, out of 540 raw layouts each, the number with a crossing is: the frozen base (the released ChiPFormer checkpoint) 42, Overwrite 108, RS 62, Cache-only 38, and CARVE 45. Legalization removes all crossings.

Q1-3: Do the main gains persist after completing and consistently legalizing the placements?

Thank you for the question. Yes. All 2,700 final layouts are complete and legal, and CARVE keeps the highest mean gain: 9.78%, versus 11.22% under the original scorer on these 18 requests. The rerun of adaptec2 and adaptec3 under their own settings is in Section 2 above; it supports the same conclusions.

4. Controlled quality–cost comparison and reused-circuit subgroup (Q2)

Q2-1: After correcting the registration issue, does a same-code, paired-seed comparison of train-each-circuit and reuse-first retain the claimed quality–cost advantage?

Thank you for the question. The training savings hold: reuse-first saves 43–62% of recorded training time, and with set A, repair time falls from 7.60 h to 4.19 h. Under the common implementation, the quality cost is 0.66–2.45 points of mean gain (Table R2). Completion and legalization add under one minute, which these times do not include.

This replay uses specialists from completed E2 runs and retrains nothing.

Q2-2: Please distinguish the reused-circuit subgroup from gains due to newly trained adaptec2.

Thank you for this request. Table R3 covers only the revisits served by another circuit's specialist. Table R4 adds adaptec2 and adaptec3, where both rules train the same new specialist, so they add exactly zero difference between the rules (Section 2 above).

In the revision. We have already added the procedure, Tables R1–R4 and the details of the adaptec2 and adaptec3 rerun to the appendix.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Thanks to all reviewers

As the rebuttal period is coming to an end, we would like to thank all reviewers for their careful reading and constructive feedback. We appreciate their recognition of the following aspects of our work:

  • The useful distinction between preserving an adapted model and authorizing its use on a particular task (7KxN, wu64).
  • The explicit statistical assumptions and matching-order validation bounds that characterize the evidence required for reliable reuse (7KxN).
  • The empirical improvements over policy overwriting (QVG3) and concrete examples of specialist reuse without access to the provider’s training data (wu64).

In our reviewer-specific responses, we have provided additional evaluations and clarified the setting, contribution, and experimental procedures. We summarize the main points below.

Complete and legal placement evaluation (7KxN, wu64). We applied a common completion and legalization procedure across methods, verified identical macro and net sets, and independently checked the resulting geometry. All 2,700 layouts in the 18-request evaluation are complete and legal. Under this evaluation, CARVE retains the highest mean HPWL gain over the frozen base: 9.78%, compared with 7.24% for Cache-only, with the method ranking unchanged.

The contribution of admission beyond model caching (wu64). To isolate admission, we held Cache-only’s specialists and evaluation cases fixed and added only the admission test. Mean HPWL gain over the 12 revisits increases from 10.86% to 11.75%, while the number of revisits performing worse than the base falls from two to zero. This comparison directly measures the contribution of validation beyond retaining trained models.

The quality–training-cost trade-off of reuse-first (7KxN, wu64). We compared train-each and reuse-first using identical code, specialist pools, and evaluation seeds. Across three specialist pools, the 18-request replay saves 42.6–61.8% of recorded training time, with a reduction of 0.66–2.45 percentage points in mean HPWL gain. The extended 24-request evaluation reports lower training savings of 31.3–46.9%, with corresponding quality differences of 0.50–1.84 percentage points. We separately report the reused-circuit subgroup; the newly trained adaptec circuits contribute no difference between the two rules. These are replay-based savings calculated from recorded training costs, rather than measurements of total deployment speedup.

The setting, positioning, and workflow (QVG3). We clarified the distinction between a task family, a request, and an evaluation case, and explained when training is triggered. CARVE’s contribution concerns the protocol and analysis for preserving adaptations, validating their suitability, and checking reuse before further training. Our response also identifies the related work and CompoNet comparison already included in the submission and consolidates the training, admission, and service procedures for both domains.

We appreciate Reviewer 7KxN’s follow-up acknowledging that the additional evaluations substantially resolve their two principal objections. Following the reviewers’ suggestions, we will further improve the manuscript by:

  • Consolidating the terminology and workflow explanations and making the relationship to prior work and existing comparisons clearer.
  • Clearly distinguishing the 18-request replay from the 24-request evaluation and labeling the original and complete/legal scoring protocols in each relevant table.
  • Keeping the lower training savings in the 24-request evaluation visible and distinguishing recorded training costs from service and validation overhead. We thank all reviewers again for helping us strengthen the empirical evidence and improve the clarity of the paper. We welcome any further questions or suggestions before the rebuttal period concludes.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.