RLVF assumes the verifier evaluates the quantity of interest. In genetic-circuit design, a topological verifier can establish that a program is a valid circuit computing the target function, whereas ranking its physical performance requires a simulator. We measure fidelity regret, the reference simple regret incurred when a cheap simulator selects the design, over a 21,362-design combination subspace spanning 5 measured gate libraries and 3 organisms. Exact ordered-assignment checks retain positive regret in every tested cell while shifting magnitudes in both directions. Mean normalized regret is 0.369 over 72 cells and only 6 have zero regret. The discrepancy depends strongly on the reference axis: the yeast library SC1C1G1T1 has mean regret 0.113 for cytometry quality and 0.801 for growth burden, and every evaluated library--circuit-size pair has positive burden regret. Topological verification ties all valid gate assignments, while an oracle whitelist subject to retaining at least 25% of the design space leaves positive regret in 30 of 52 cells. Design-space optimization and feedback-guided search with frozen language models reach the high-regret regions; on a matched zero-regret control, additional optimization instead reduces regret. At a matched modeled-cost budget, mitigation is budget- and library-dependent. An in-sample fixed rule spending α=0.34 of the budget re-scoring top cheap-simulator designs achieves mean excess regret 0.016, compared with 0.305 for cheap-only and 0.034 for reference-only selection, improving on cheap-only in 330 of 360 cells. More broadly, any workflow optimized through a simulator or digital twin can satisfy its verifier yet perform poorly on the intended physical objective. Fidelity regret provides a transferable template for detecting this gap before optimization and comparing budget-aware remedies across scientific domains.
Figures & tables
Figure 1: Exact fidelity regret with L1 as the reward. (a) Normalized regret for each (library, k , topology) cell; the dashed line is the L0 uniform-tie-break expectation, 0.541. (b) Percentile of the L1-selected design under each reference. Panels c–d appear in Fig. 3 .
Figure 2: Optimization and mitigation results. Panels (a,b) show regret incurred; panels (c,d) show regret recovered on an axis unbounded below. (a) Design-space search, 30 seeds per arm. (b) Frozen-model search at maximum pressure; (c,d) Eight rewards at a matched modeled-cost 2.0 s purse, 40 runs per cell. L2 discrepancy cells are marked not affordable .
Appendix figures & tables23 assets
Supplementary material from the paper’s appendix.
Appendix
Library
Organism
Gates
Hill
Cytometry
Toxicity
τ
Levels
Eco1C1G1T1
E. coli NEB 10-beta
20
20
20
20
0
L0–L4 †
Eco1C2G2T2
E. coli NEB 10-beta
18
18
18
18
18
L0–L4
Eco2C1G3T1
E. coli MG1655 K-12
6
6
6
6
0
L0–L4 †
SC1C1G1T1
S. cerevisiae BY4741
12
12
12
12
0
L0–L4 †
Bth1C1G1T1
B. thetaiotaomicron
7
7
0
7
0
L0,L1,L3,L4 †
Appendix
Table 1: Per-library coverage. Bth1C1G1T1 ships growth-burden tables for all seven gates but no single-cell cytometry, so the cytometry references (L2, L2 d′ and the joint L2+L3 references) are unsupported there; L3 and L4 are supported. The τ column counts gates with measured τon/τoff values; † denotes library-default kinetics.
Figure 3: Full four-panel version of Fig. 1 . (c) Worst normalized regret per library × reference with the group minimum beneath, bold where it is exactly zero; Bth1C1G1T1 cytometry cells are n.d. because cytometry is unsupported. (d) Fraction of achievable growth-burden quality kept on each library’s worst cell, annotated with the gate the cheap score recruits and the oracle avoids.
Library
L2 (cyt. quality)
L2 d′ (cyt. sep.)
L3 (burden)
L4 (kinetics)
Eco1C1G1T1
0.536
0.687
0.908
0.863
Eco1C2G2T2 ∗
0.514
0.516
0.290
0.452
Eco2C1G3T1
0.470
0.431
0.852
0.926
SC1C1G1T1
0.133
0.230
0.999
0.938
Bth1C1G1T1
n.d.
n.d.
0.630
0.870
Appendix
Table 2: Worst normalized regret per library and reference axis, L1 paying the reward. n.d. = the reference is not evaluable for that library. ∗ carries the Eco1C2G2T2 UCF defect flag (§ G ).
Figure 4: (a) Spearman rank correlation between fidelity levels on each library’s gate set. (b) Cost per evaluation relative to L0, log axis.
Timing basis
Measures
L2 (s)
L2/L1
L3/L1
Standalone benchmark
isolated per-evaluation, all 5 levels
0.086403
94.3
3.9
In-loop cost model
optimization-loop execution, L0–L3
0.063297
67.4
2.2
Appendix
Table 3: The two measured cost bases. Every budget comparison in this paper uses the in-loop exchange rates ; the standalone benchmark supplies the relative-to-L0 ladder in Fig. 4 b.
Figure 5: (a) Worst normalized regret per library on cytometry and burden; two E. coli libraries land at opposite ends. (b) Discrepancy-model R2 across four splits: L2 includes negative values under shift, whereas L3 remains positive. (c) R2 on optimizer-returned designs: L2 median 0.212, L3 median 0.740.
Split
L2 cytometry quality
L3 growth burden
random
0.520 – 0.972
0.898 – 0.988
topology_holdout
−0.036 – 0.887
0.780 – 0.976
shift_q90
−1.334 – 0.699
0.379 – 0.991
shift_q99
0.409 – 0.857
0.856 – 0.996
optimizer-returned (median)
0.212
0.740
Appendix
Table 4: Gradient-boosted discrepancy-model R2 , range across libraries. L2 includes negative values under distribution shift; L3 remains positive.
Figure 6: Range-normalized regret against optimization pressure for the frozen models. Regret rises under optimizers that feed the cheap score back into the prompt and does not rise under pure best-of- n selection. Range-normalized regret Rrange∈[0,1] (§ C ) remains well defined on the zero-enumerated-regret cell of the falsification control, where a cheap-optimum-relative fraction has a zero denominator.
Variant
Reference
Absolute regret
Percentile of pick
Spearman
as published
L2
1.176
64.8
0.531
corrected
L2
0.879
84.3
0.593
as published
L3
0.166
97.1
0.063
corrected
L3
0.166
97.1
0.063
Appendix
Table 5: Eco1C2G2T2 sensitivity to the decimal defect. The L3 result is unaffected; the L2 result changes materially, so both are reported.
SC1C1G1T1
Eco1C2G2T2
Reward variant
L3 burden
L2 cytometry
L3 burden
L2 cytometry
cheap L1 (naive)
0.007
−0.720
−0.724
0.155
reference simulator
0.944
−2.168
0.555
0.433
ensemble mean, M=8
0.065
−1.011
−1.925
0.149
ensemble mean −1σ
0.123
−2.475
−2.124
0.111
ensemble CVaR 0.05
0.152
−3.499
−1.978
0.063
Appendix
Table 6: Fraction of achievable regret recovered at a matched modeled budget equivalent to 2.0 s, mean [95% CI] over 40 runs. infeasible indicates that the declared acquisition cost exceeds the full budget and permits no training calls.
Schedule
switch
L3 recovered [95% CI]
vs cheap_only ( p )
cheap_only
–
0.007 [ −0.036 , 0.050]
–
reference_then_cheap
0.50
0.169 [0.093, 0.250]
+0.162 ( <10−4 )
interleaved
0.50
0.641 [0.540, 0.739]
+0.634 ( <10−4 )
cheap_then_reference
0.75
0.618 [0.506, 0.733]
+0.611 ( <10−4 )
cheap_then_reference
0.50
0.783 [0.697, 0.861]
+0.776 ( <10−4 )
cheap_then_reference
0.25
0.890 [0.853, 0.926]
+0.883 ( <10−4 )
Appendix
Table 7: Curriculum schedules on SC1C1G1T1 at the matched budget. The reference_only row provides the direct-reference comparator.
Figure 7: Fidelity curricula on SC1C1G1T1 (the only library swept), 40 runs per point at the matched modeled budget equivalent to 2.0 s. (a) Against growth burden every mixed schedule beats cheap-only; against cytometry quality none does, and reference_only has negative recovery. (b) On growth burden (L3), every cheap-first schedule lies below the reference_only line. On cytometry quality (L2), the ordering inverts because reference_only is harmful there. The recovery axis is unbounded below.
Model
Fresh calls
Input tokens
Output tokens
List cost (USD)
Haiku 4.5
182
840,626
95,844
1.32
Opus 4.5
164
760,515
56,453
5.21
Sonnet 4.5
165
182,683
66,000
1.54
Total
511
1,783,824
218,297
8.07
Appendix
Table 8: Frozen-model spend at public list prices. Totals are 511 fresh calls, 2.00M tokens, $8.07.
Library
Topology
Ordered designs
Reference
Combination
Ordered
Eco2C1G3T1
chain_k4
360
L2
0.470
0.118
Eco2C1G3T1
chain_k4
360
L2 d′
0.431
0.229
Eco2C1G3T1
chain_k4
360
L3
0.547
0.436
Eco2C1G3T1
chain_k4
360
L4
0.926
0.506
SC1C1G1T1
chain_k3
1,320
L2
0.133
0.139
SC1C1G1T1
chain_k3
1,320
L2 d′
0.230
0.302
Appendix
Table 9: Range-normalized regret on the combination subspace and the fully enumerated ordered-assignment space.
Library
Topology
Reference
Absolute lower bound [bootstrap]
Normalized
Eco1C1G1T1
chain_k4
L2
0.164 [0.091, 0.164]
0.059
Eco1C1G1T1
chain_k4
L2 d′
0.502 [0.258, 0.502]
0.107
Eco1C1G1T1
chain_k4
L3
0.327 [0.299, 0.327]
0.257
Eco1C1G1T1
chain_k4
L4
0.100 [0.091, 0.100]
0.264
Eco1C1G1T1
xnor_k4
L2
0.171 [0.142, 0.171]
0.066
Eco1C1G1T1
xnor_k4
L2 d′
0.392 [0.303, 0.392]
0.087
Appendix
Table 10: Ordered-assignment checks for Eco1C1G1T1 , with 116,280 designs per cell. The cheap argmax is exact; the reference statistics use a sample of 4,001 designs.
Library
V0 gate-blind
V1 blacklist
V2 growth floor
V3 quality floor
V4 oracle
Bth1C1G1T1
0.346
0.150
0.150
0.273
0.035
Eco1C1G1T1
0.383
0.172
0.174
0.381
0.036
Eco1C2G2T2
0.208
0.120
0.175
0.157
0.089
Eco2C1G3T1
0.636
0.314
0.314
0.636
0.314
SC1C1G1T1
0.801
0.655
0.655
0.741
0.066
Appendix
Table 11: Normalized regret under each verifier class against growth burden (L3), best parameter subject to admitting ≥25% of the space, averaged over topologies. V4 is the non-implementable oracle whitelist and therefore an upper bound on the whole class.
Figure 8: Fidelity regret under each verifier class as a function of how much of the design space the verifier admits. The oracle whitelist (V4) is a non-implementable upper bound on the per-gate-admissibility class; it flattens well above zero in most cells.
Figure 9: Cheap discrepancy-predicting features used as free constraints, against paid baselines. The best free method beats the naive baseline in 11 of 13 library-by-axis cells, at a median of 4.0 reference calls to match.
Figure 10: Regret against budget for each allocation policy. The adaptive multi-fidelity methods and the best simple policies have similar frontiers.
Figure 11: Sentinel detection rate against cost, as a fraction of a full reference sweep.
Figure 12: The decision procedure and its validation against the enumeration.
Figure 13: Cost of the Rule-S diagnostic as a fraction of the advised budget, and the cells where it converges on the wrong action.
Figure 14: Change in normalized regret from each robust objective, relative to the naive point-estimate pick.
Genetic circuit design remains a laborious, expert-driven process despite decades of progress in synthetic biology. We study this problem through code generation: models produce Python code in pysbol3 to construct genetic circuits in the Synthetic Biology Open Language (SBOL), a formal representation that supports automated verification. We introduce GenCircuit-RL, a reinforcement learning framework built around hierarchical verification rewards that decompose correctness into five levels, from code execution to task-specific topological checks, and a four-stage curriculum that shifts optimization pressure from code generation to functional reasoning. We also introduce SynBio-Reason, a benchmark of 4,753 circuits spanning six canonical circuit types and nine tasks from code repair to de novo design, with held-out biological parts for out-of-distribution evaluation. Hierarchical verification improves task success on functional reasoning tasks by 14 to 16 percentage points over binary rewards, and curriculum learning is required for strong design performance. The resulting models generate topologically correct circuits, generalize to novel biological parts, and rediscover canonical designs from the synthetic biology literature.
Simulation success is not equivalent to structural correctness for LLM-generated circuits. We define and measure four evaluation levels -- schema validity, topological validity, backend executability, and component-set agreement -- on a 150-circuit trilingual benchmark, through a deployed pipeline built on a typed circuit interchange representation. The levels are not nested. On gpt-4o-mini, 16 of 150 circuits (10.7%, 95% CI 6.7-16.6) were rejected by the topological validator but executed in ngspice with no error or warning; 12 of these contained exactly the requested components, with one terminal disconnected. Conversely, 7 circuits (4.7%) passed the validator and ngspice refused them. Ten failed both checks and 117 passed both, so each check detects a class the other misses. A minimal three-component divider shows the cost: a dangling resistor reports 5.00 V instead of 2.50 V while ngspice stays silent. A paired ablation, in which every arm is evaluated from the same model sample rather than a fresh one, separates each repair stage from sampling noise. On a stratified 45-circuit subsample, model repair raised topological validity from 40.0% to 84.4% (+20 circuits, no regressions) while moving executability by a net 6 (+7, -1), an effect this sample size does not resolve, and component agreement by 2. One circuit moved in opposite directions at two levels in a single repair step. Against a direct-netlist baseline the pipeline executed 88.7% against 47.3%, or 62.7% under an accounting that credits the baseline with every failure we cannot confidently attribute to the netlist. These results support a narrow methodological conclusion: structural validation and simulation should be reported as distinct evaluation stages for LLM-generated circuits. A circuit that runs is not necessarily structurally valid, and a structurally valid circuit is not necessarily executable.
Synthesis pipelines increasingly claim not just that a program is correct, but that it is optimal. Such a claim has two halves with radically different verification stories. The upper bound, "a program of size m exists", is witnessed by an artifact that can be re-executed, proved equivalent to its specification, and shipped with a machine-checked certificate. The lower bound, "no program of size m-1 exists", has no witness and is discharged by running a solver until it reports UNSAT. Combinatorial optimization has known this asymmetry for decades and has largely addressed it: certifying algorithms make it explicit (McConnell et al., 2011), and pseudo-Boolean proof logging can certify optimality end to end with a formally verified checker (Bogaerts et al., 2023; Koops et al., 2025). That discipline has not reached circuit minimization. We call this the refutation gap: published gate counts for minimal XOR circuits provide no certificate for either half of the claim, and neither did 121 optimality results we ourselves produced. We close the gap with a pipeline that synthesizes minimal linear straight-line programs over GF(2), where every decisive UNSAT answer emits a DRAT proof checked by an independent third-party checker. We certify all 121 optimality results established by the project, across n = 6 to 9: 111 carry independently verified refutations, 10 are closed by a free counting bound, and none disagrees with the uncertified value. The median proof is 1.1 MB and checking costs 1.9x solving. We give five case studies where verification caught defects that code review did not, report two interface obstacles that push practitioners toward the uncertified path, and describe an adversarial audit that revealed a failure tail we were about to attribute to the problem was actually caused by our own budget.