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Paper summary
ArrivalFM-OTA presents a dataset containing 2,649,573 Spectre simulation records for 28 OTA topologies and 10 FinFET technology models for prediction purposes, where 2,059,328 simulation records are grouped to create a benchmark with 68 global and device-level predictions. The paper also presents a residual augmentation called DAWN, which helps in device operating point and circuit performance prediction. Experiments across four neural backbones and 10 initialization seeds demonstrate improvements on known topologies and a held-out technology model.
Critical strengths
S1. The dataset offers abundant supervision for circuit representation learning.
The fact that there is information on circuit performance, internal operating state of transistors, and failure related target under different environmental settings makes a valuable contribution. It helps in understanding the study on the relationship between local behavior and global circuit performance, which is hard to conduct using datasets that provide only aggregate metrics.
Critical weaknesses
W1. The contribution of the DAWN methodological insight with respect to multitask residual augmentation is not clear.
The baselines already receive device-level supervision, while DAWN incorporates increased capacity and modifies how the global context is incorporated into the representations for the task of circuit prediction. The results presented do not separate the impact of these modifications from the introduced physical-conditioning process. Furthermore, the circuit-level predictor utilizes shared latent representations instead of explicit prediction of the operating point, which is not obvious because of the terminology used in the paper ("waypoint" and "physics-conditioned"). This is worsened by the dense formulation, where numerous equations and implementation details do not lead to an understanding of the physical dependency captured and how and when it is verified.
W2. The benchmark’s physical validity and the interpretation of its evaluation metrics require stronger justification.
There are still several points related to data and assessment which require further explanation. Section 3.2 does not explain how the entire data set is used to form the benchmark subset. Appendix E.2 introduces physical failures, numerical failures, and intentionally skipped analyses, while several classification targets in Table 23 use the availability of metrics as criteria for classification. Thus, the average classification accuracy alone does not mean reliable detection of physically invalid circuits. Moreover, Table 22 states the maximum static power of W and mean power of 1244.12 W, but the median power is W, requiring a clear physical analysis of the benchmark selection criteria. These points do not mean the inappropriate nature of the PTM-based data, but they cast doubts about the goals of the benchmark.
Questions for authors
Q1. Clarification. Methodological evidence.
Given that the baseline models already receive device-level supervision, what evidence attributes DAWN’s gains specifically to learning physical intermediate states? Does the advantage persist against a parameter-matched residual baseline with equivalent access to global context, and how does removing device-level supervision affect that comparison?
Q2. Clarification. Physical pathway.
Global predictions in Equations 6 and 7 make use of a latent residual that is common to all of them rather than predictions of operating point values directly. What is the characteristic of this approach that can be used to explain why it may be called physical intermediate-state cascade and what proof exists for the usage of learned device physics in global predictions? How can we justify the statement about zero initialization “completely preventing auxiliary gradient interference”?
Q3. Clarification. Validity of benchmarks.
Why is there a very high power in Table 22, and are the associated data kept in the training and validation sets? Please specify how the 2,059,328 benchmarking data samples are selected, and if any improvement in the results can be observed by removing artifacts.
Q4. Clarification. Failure prediction accuracy.
How does Table 23’s labeling distinguish intentionally skipped analyses from physical failures, particularly when periodic analysis is skipped because unity-gain bandwidth is at most 1 kHz? What are the class frequencies and precision and recall of failure classes after making such a differentiation? How should classification accuracy be evaluated without making such a differentiation?
5 comments
Response To Reviewer mU6C (W2, Q3)
W2 & Q3: We thank Reviewer mU6C for these vital questions regarding dataset partitioning and dataset convergence artifacts.
In Section 1 (Pages 1-3) and Section 3.2 (Page 5), we clarify that the standardized ArrivalFM-OTA benchmark consists of 2,059,328 simulation records, gathered from running data collection for each of our 28 OTA topologies strictly following Algorithm 1 (Section 3.1, Page 4). The remaining 590,245 datapoints in our dataset represent 100% physically valid Spectre simulations from early exploratory sizing sweeps, which are released alongside our open-source Contact synthesis framework as an unpartitioned archive for open self-supervised pretraining. The 2,059,328 benchmark datapoints are then partitioned into Training, Validation, and 4 standardized Test splits, as defined in Table 2 (Section 3.2, Page 5).
Power consumption across ArrivalFM-OTA is physically grounded and tightly clustered around a median of P = 0.371 mW with an interquartile range of IQR = 2.16 mW, where over 99.5% of evaluated designs draw less than 4.74 mW. The divergence in the arithmetic mean P = 1244.12 W and maximum value W arises from a numerical Spectre solver artifact affecting exactly 309 of 2,059,328 total benchmark samples, occurring exclusively within unfeasible designs of a single topology, OTA_FD03. DC open loop gains for these 309 samples range from -134.09 dB to -11.15 dB, drawing from 50.06 mW to 976.21 MW of power. We hypothesize that severe voltage headroom starvation in OTA_FD03's 5-transistor stack under unclamped ideal common-mode feedback (CMFB) caused simulator divergence on the auxiliary supply current variable V0:p. Furthermore, physical transistor currents in these exact simulations remained below 3.71 mA. These design points are intentionally retained in the benchmark as negative training samples for feasibility classifiers and component-level metric regressors. We have included this explanation of these anomalies in the description of Table 23 (Appendix F, Page 48).
Additionally, in direct response to your question regarding whether removing artifacts improves performance: because neural surrogate models optimize Z-score normalized loss objectives and are evaluated via rank-based and median statistics, these 309 non-convergent points do not destabilize model training or corrupt median metrics. As reported in Table 6 (Section 5, Page 10), our DAWN GCN achieves a static power physical MedAE of 103.37 ± 1.83 µW (R² = 0.9562 ± 0.0041) across all 161,160 in-distribution test samples. However, unweighted arithmetic MAE is inherently vulnerable to extreme numerical outliers. As explicitly detailed in Footnote † of Table 6, when static power physical MAE is evaluated across the remaining 19 in-distribution topologies excluding OTA_FD03, DAWN GCN achieves an MAE of 879.24 ± 23.90 µW, directly matching physical sub-milliwatt circuit scales. In sharp contrast, if OTA_FD03 is included, the arithmetic physical MAE across the test set explodes to 204.51 W, driven entirely by those divergent simulator artifacts. Removing this single artifact topology reduces the physical MAE by more than five orders of magnitude (from 204.51 W down to 879.24 µW), verifying that model predictions outside this simulator singularity remain physically faithful.
Response To Reviewer mU6C (W2, Q4 Part I)
W2 & Q4: We thank Reviewer mU6C for their critique regarding the semantic distinction between physical circuit failures, simulator numerical divergences, and intentionally bypassed analyses. We fully agree that evaluating surrogate fidelity solely via aggregate macro accuracy could obscure failure-mode detection if criteria were conflated.
We have revised our description of classifier heads in Table 24 (Appendix G, Page 50) to provide insight into our reasoning for introducing classifier heads as a universal diagnostic for defined NaN failures in Appendix D.2 (Pages 31-34) and Appendix E.2 (Pages 36-37). Downstream analyses such as large-signal dynamic swing (swing_stab), DC offset (offset_stab), transient settling envelopes (transient_sr, transient_sf, transient_lr, transient_lf), and periodic steady-state analysis (periodic_stab) are trained to classify an OTA design as invalid (0) if a candidate fails an upstream AC/DC gatekeeper as described in Appendix E.2 or fails to return a valid result given target performance metric definitions in Appendix E.3 (Pages 37-44). Specifically, for periodic steady-state analysis, we require Cadence Spectre's harmonic shooting algorithm to have a stabilization time of . When unity-gain bandwidth collapses below 1 kHz, the required stabilization window extends to , which we observe commonly causes divergence errors and excessive CPU timeouts. Thus, each head acts as an independent, domain-specific feasibility filter for determining whether a candidate sizing yields valid, non-divergent specifications within that respective characterization domain, while complete end-to-end simulation convergence is independently isolated by the validity head, conditioned on sim_status as defined in Table 21 (Appendix E.2, Page 37). Notably, sim_status retains nominal validity even when simulation stages are declared as invalid under the ≤ 1 kHz constraint.
To directly address your question regarding class frequencies and whether accuracy is inflated without differentiating failure classes, we have added Table 30 (Appendix I, Page 57), which reports decoupled performance across all 10 individual classification heads for the DAWN GCN baseline as mean ± standard deviation across 10 random initializations:
| Classifier Head | Ground Truth Positive Rate | Predicted Positive Rate | Classification Accuracy | Precision | Recall | -Score |
|---|---|---|---|---|---|---|
validity | 63.24% | 64.67% ± 0.34% | 94.79% ± 0.06% | 0.9488 ± 0.0027 | 0.9701 ± 0.0024 | 0.9593 ± 0.0004 |
nominal_stab | 67.55% | 68.71% ± 0.27% | 96.16% ± 0.05% | 0.9636 ± 0.0021 | 0.9801 ± 0.0017 | 0.9718 ± 0.0004 |
threshold_stab | 95.24% | 95.38% ± 0.15% | 99.12% ± 0.02% | 0.9946 ± 0.0008 | 0.9961 ± 0.0008 | 0.9954 ± 0.0001 |
swing_stab | 61.29% | 62.37% ± 0.35% | 95.44% ± 0.05% | 0.9547 ± 0.0028 | 0.9717 ± 0.0027 | 0.9631 ± 0.0004 |
offset_stab | 61.29% | 62.38% ± 0.35% | 95.44% ± 0.05% | 0.9547 ± 0.0028 | 0.9717 ± 0.0027 | 0.9631 ± 0.0004 |
periodic_stab | 60.63% | 61.94% ± 0.38% | 94.69% ± 0.08% | 0.9466 ± 0.0031 | 0.9669 ± 0.0029 | 0.9566 ± 0.0006 |
transient_sr | 60.04% | 61.60% ± 0.39% | 93.64% ± 0.06% | 0.9357 ± 0.0029 | 0.9600 ± 0.0031 | 0.9477 ± 0.0005 |
transient_sf | 60.63% | 62.28% ± 0.37% | 93.55% ± 0.06% | 0.9350 ± 0.0026 | 0.9604 ± 0.0031 | 0.9475 ± 0.0005 |
transient_lr | 50.45% | 51.61% ± 0.39% | 92.57% ± 0.06% | 0.9168 ± 0.0030 | 0.9379 ± 0.0042 | 0.9272 ± 0.0008 |
transient_lf | 46.74% | 47.99% ± 0.39% | 92.20% ± 0.08% | 0.9057 ± 0.0032 | 0.9300 ± 0.0045 | 0.9177 ± 0.0010 |
Response To Reviewer mU6C (Introduction, W1, Q1, Q2)
We would like to thank Reviewer mU6C for their rigorous and insightful critique of our submission. We are grateful for your recognition of dataset scale and the value of providing dense multi-task supervision spanning circuit performance, internal device operating states, and characterization flags under environmental sweeps. We are especially appreciative of your audit regarding classification criteria and numerical artifacts in our benchmark and dataset, both of which have been clarified in revised versions of Section 1 (Pages 1-3), Appendix F (Pages 45-48), Appendix G (49-51), and a newly instantiated Appendix I (Pages 57-60).
W1 & Q1: We thank Reviewer mU6C for their raising this point. We agree with your assessment: because baseline models already receive device-level supervision, our original manuscript blurred the distinction between targeted bottleneck capacity and multi-task guidance. In direct response to your question: we do not have an existing baseline that isolates the +148,224 parameter bottleneck (+0.15M weights) from auxiliary device supervision, nor an ablation removing device supervision from the bottleneck.
Consequently, we do not claim that DAWN's gains stem from an isolated physical mechanism independent of capacity. In standard baselines, device-level supervision and global specification predictions are decoupled into independent heads operating on the final backbone representation hv(L). DAWN modifies this by injecting an auxiliary-guided latent residual stream into the shared representation. Its empirical lift reflects the combined benefit of this targeted bottleneck capacity and multi-task guidance. Two empirical findings clarify this role.
First, adding DAWN's +148k parameter bottleneck and auxiliary supervision to our nonrelational MLP baseline yields only +0.0150 R², contrasting with +0.0437 R² across a parameter-matched, graph-based GCN backbone. This demonstrates that while added capacity yields a minor baseline lift, DAWN’s empirical gain is strongly amplified by relational component connectivity.
Secondly, R² gains are not uniform across targets as would be expected from generic capacity expansion. In our revised manuscript, we have added Table 32 (Appendix I, Page 59) establishing a full per-metric breakdown of R² gains across our DAWN ablations. Please see our posted comment Response To Reviewer 1ZSL (W3, Q1 Part I) for exact numerical details.
W1 & Q2: We thank the reviewer for highlighting these distinctions. Your observations are correct: the circuit-level predictor utilizes a shared continuous latent residual rather than explicit numerical operating points, and zero-initialization does not prevent auxiliary gradient flow during training. We have updated Section 4.2 (Page 7) to state this explicitly: zero-initialization "preserves the backbone’s initial forward mapping. Although auxiliary heads still backpropagate gradients through the identity path, this zero-initialization prevents uninitialized projections from destabilizing early training across all four evaluated backbones".
We also concede that calling DAWN a "physical intermediate-state cascade" and utilizing vocabulary such as "analog waypoints" or "physics-conditioned" was misleading. In reality, global readouts make use of a continuous latent residual vector Δv∈R512 that is shared across heads. In the revised manuscript, we have systematically removed those terms describing DAWN across the Title, Abstract, Section 1, Section 4.2, Section 5 (Pages 8-10), and Appendix H.2.5 (Page 56), and concede that there is no causal proof that the global readout head explicitly uses learned device physics beyond standard multi-task latent representation sharing. We now describe DAWN objectively as an additive multi-task residual regularizer rather than an autonomous physical solver, and instead focus our analysis on the empirical benefit of DAWN as a whole and the narrowed zero-initialization guarentee. We have also revised our description of DAWN regarding DC operating points (DCOP) as a DCOP-Aware Weighted Network, from its original description of DCOP Analog Waypoint Nodalization, to more accurately reflect technical reality, and added Figure 21 (Appendix I, Page 56) as an informative visual reference of the DAWN framework.