Training Scientific Agents to Learn from Physical Experiments
TL;DR
SDL-1 showed that frontier models could run experimental campaigns without reliably learning from the evidence they acquired. We trained scientific judgment in a 35B open model on replay environments compiled from lab experiments, then scaled inference. The final system completed every campaign, kept its claims within the measured evidence boundary, improved forecasts about unseen chemistry, and reached the open-weight frontier on SDL-1.
Scientific agency begins when evidence from one campaign improves the judgment applied to the next. The report covers how we built that loop, from the staged training recipe and reward design to the trace-driven inference changes behind the final system.
Scientific agents that direct self-driving laboratories run experiments and decide what to run next, which evidence to trust, and what to optimize when the useful search space is only partly defined. We post-trained a 35B-total, 3B-active open-weights policy initialized from Qwen3.6-35B-A3B to improve scientific judgment. This study targets a bounded part of that capability, evidence-conditioned campaign control after the objective and candidate experiments are fixed.
The Precursor Genome records all 1,035 unordered pairs among 46 inorganic precursors, with execution metadata, X-ray diffraction, automated refinement, and expert phase assignments. SDL-1 compiles that experimental record into a partially observable campaign environment. The policy sees only the evidence it acquires, chooses experiments under a fixed budget, and receives scores from recorded outcomes held private by the evaluator.
Our first SDL-1 report found three failures across every frontier system we evaluated. Policies made claims beyond their evidence. Local and held-out forecasts moved in opposite directions in 145 of 293 scored updates, and experiment-selection lift changed sign across benchmark assignments. Those failures became the behavioral axes for this study.
Training and added inference moved adaptive AUC from −1.893 for the base policy to −1.466 for the final system. SDL-1 reports negative held-out log loss, so zero is the ceiling and higher values are better. The final system placed above GLM 5.2 at −1.528 in the descriptive comparison.
No eligible scored belief row triggered the unreviewed-refinement overclaim indicator, all 234 eligible belief-update actions passed first-pass validity, and endpoint gain reached +0.023. Experiment selection remains unresolved at +0.009, inside evaluation noise.
Why Train
Before changing the weights, we asked whether more inference could make a frozen frontier policy reliable. We placed DeepSeek V4 Flash inside a recursive self-improvement loop that replayed complete SDL-1 campaigns, used recorded outcomes to locate decision errors, and searched for better ways to use evidence and select experiments.
Useful scientific behavior appeared, but the loop did not make it dependable across campaigns. The Qwen base policy showed the same ceiling. Valid-action coverage, which measures whether the policy can produce a benchmark-legal action, rose from 59.0% on the first sample to 62.4% after four samples, and the fourth sample recovered no additional actions.
Bayesian optimization already solves an important part of this problem by updating a surrogate model, often a Gaussian process, and using an acquisition rule to choose the next experiment for a defined objective. Benchmarking Self-Driving Labs measures its value in experiments saved or performance gained against a reference campaign. Multi-stage Bayesian optimization extends this loop to intermediate measurements and flexible workflows.
We train the campaign policy around that optimizer. It must decide which evidence bears on the engineering decision, whether a result is trustworthy, which beliefs should change, and whether the campaign should commit, continue, or pivot. Its goal is decision-ready evidence, a traceable record sufficient for a specified engineering action. BO remains one of the tools the policy can use.
The Environment
To train scientific judgment, we need to know what the policy knew, what it chose, how certain it was, and what happened next. Compiling the Precursor Genome into SDL-1 adds this decision record to the physical one and turns a completed campaign into a replayable sequence of choices under uncertainty.
The environment keeps the policy’s view separate from the full experimental record, so the recorded outcome can grade a decision without entering the state that produced it.
Replay changes the decision path while keeping the physical record fixed. A policy may inspect different evidence, spend its budget on another branch, or update a different set of beliefs.
Two policies can reach the same conclusion for different reasons, and only the trace shows whether the evidence supports making that decision again. The evaluator can locate the failure in an unsupported claim, an update that did not transfer, or a decision that did not improve. Each failure becomes a separate learning signal.
Alongside measurements, the resulting corpus preserves the lineage of evidence, uncertainty, decisions, and consequences that shaped each campaign. Once a physical outcome exists, replay can provide near-immediate feedback on how a policy reached its conclusion. As policies learn, the corpus grows in both physical outcomes and decision traces.
Training
A campaign does not contain one kind of decision. The policy must produce a valid action, decide how new evidence changes its beliefs, preserve claims that the evidence does not affect, and carry those choices into later experiments. One final score would hide which of these behaviors failed.
The training stages formed one sequential lineage. Each stage continued from the selected checkpoint produced by the stage before it, with no checkpoint merging, and widened the part of the campaign for which the policy was responsible.
Supervised Fine-Tuning for Valid Actions
The base policy could sample useful scientific actions, but it did not produce them reliably on its first attempt. We used best-of-k rejection sampling to move those rare actions toward the policy’s default behavior.
For each training state, the policy generated several candidates. A frozen evaluator admitted only actions that satisfied the schema, cited valid evidence, respected provenance, and could be replayed. We trained on the admitted actions.
The natural candidate set was dominated by safe no-change decisions. Left alone, this would reward caution as inaction. We balanced the training mixture across physical updates, expert-licensed updates, correct no-change decisions, exact preservation of unaffected beliefs, and calibrated forecasts.
This stage did not meet its specified success threshold. We treated it as a stronger starting policy, not as evidence of campaign control.
Process RL for Local Credit
Once the policy could produce valid actions, the main problem became credit assignment. If a forecast improves after several evidence updates, the final score does not tell us which earlier decision deserves credit.
We used REINFORCE Leave-One-Out (RLOO) to compare actions sampled from the same campaign state and turn.1 Reward-to-go assigned each action the later rewards it preceded, then RLOO compared that return with the other actions from the same state and turn. Credit remained tied to measured campaign outcomes without a learned value model.
Clipped Importance Sampling Policy Optimization (CISPO) bounded the influence of extreme sample-to-train importance ratios while keeping the token gradient active.2
Before using this recipe for training, we ran a zero-gradient comparison on fresh trajectories. It confirmed that matched campaign states produced a usable relative reward signal and that sample-to-train drift was small. CISPO clipping was rarely active, so we treat it as a stability guard rather than the source of the final performance gain.
Campaign RL Across Experiments
We then widened the horizon from one evidence update to one- and two-experiment campaigns. The policy chose evidence, allocated expert review, updated or preserved its beliefs, and made later forecasts.
The same reward-to-go rule assigned later rewards to the earlier actions that preceded them. This allowed a forecast near the end of a campaign to provide credit to an earlier evidence choice or belief update.
An update required at least six of eight same-state groups to contain two or more valid terminal trajectories. Every selected batch passed this gate, and weaker groups still contributed after the batch passed.
This stage showed partial composition across short campaigns. Training covered at most two experiments, and the environment had no authoritative measure of downstream utility or optimal stopping, so it did not establish reliable long-horizon control or optimal stopping.
Outcome-Grounded RL for Evidence Assimilation
A final RL continuation held experiment selection fixed and trained evidence assimilation and claim scope against evaluator-private recorded outcomes. Its reward separated evidence-conditioned campaign control into behaviors that the evaluator could verify. The six positive coefficients formed the composite reward, while an invalid action received a separate penalty.
| Reward signal | Behavior reinforced | Coefficient or penalty |
|---|---|---|
| Evidence-licensed claims | Change only claims supported by acquired evidence | 0.20 |
| Recorded-outcome forecast | Assign probabilities that agree with the recorded physical result | 0.20 |
| Exact preservation | Keep unaffected beliefs unchanged | 0.15 |
| Correct no-change decision | Abstain when the evidence does not license an update | 0.15 |
| Expert-review value | Estimate whether expert review could change the decision | 0.10 |
| Future-chemistry forecast | Carry acquired evidence into later predictions | 0.20 |
| Invalid policy action | Reject an action that breaks the campaign contract | −1.00 |
Recorded outcomes affected reward and weight updates but remained private to the evaluator.
Deterministic checks took priority over semantic scoring. A fluent explanation could not compensate for an unsupported claim, an invalid action, or a forecast change outside the evidence boundary.
(a) Supervised negative log-likelihood
Each point is an equal-weight mean over eight training examples. It is not held-out or token-weighted. Each segment starts a new corpus, learning-rate schedule, and optimizer. Segment 3 also changes the instruction format.
S1 · updates 1–40n=40 · LR 1e-4
S2 · updates 41–70n=30 · LR 3.0e-5
S3 · updates 71–80n=10 · LR 0.5e-4
(b) Trajectory rewards by curriculum
All 64 trajectory rewards are shown for each curriculum. The populations and applicable reward axes differ. Curricula are not connected and do not form a learning curve.
(c) Stability diagnostics by curriculum
Dots share a scale only within each column. Exact values are shown. The sampled-token count is the clipped-rate denominator. These are stability checks, not task-improvement trends.
| Curriculum | KL v2 ×10⁻³ | Entropy | Clipped tokens | Sampled tokens |
|---|---|---|---|---|
| Expert updates | 1.463 | 0.148 | 1 | 504,887 |
| No-change curriculum | 1.631 | 0.164 | 3 | 432,555 |
| Physical updates | 1.430 | 0.155 | 0 | 415,364 |
| Exact preservation | 1.486 | 0.159 | 0 | 412,631 |
| Future forecast | 1.532 | 0.150 | 1 | 498,033 |
(d) Training-signal coverage
A valid terminal completed all three protocol actions, ended the episode, and had no hard failure. A qualified group had at least two valid terminals. All selected batches passed the batch-level gate. No batch was rejected.
| Curriculum | Valid terminals | Qualified groups |
|---|---|---|
| Expert updates | 28/64 | 8/8 |
| No-change curriculum | 37/64 | 8/8 |
| Physical updates | 28/64 | 7/8 |
| Exact preservation | 40/64 | 8/8 |
| Future forecast | 30/64 | 6/8 |
Exact data
| Update | Curriculum | Reward mean | Median | IQR | KL v2 | Entropy | Clipped | Valid | Groups |
|---|---|---|---|---|---|---|---|---|---|
| 1 | Expert updates | −0.779 | −1.000 | −1.215 to −0.268 | 1.463×10⁻³ | 0.148 | 1/504,887 | 28/64 | 8/8 |
| 2 | No-change curriculum | −0.624 | −0.434 | −1.057 to −0.254 | 1.631×10⁻³ | 0.164 | 3/432,555 | 37/64 | 8/8 |
| 3 | Physical updates | −0.406 | −0.650 | −1.000 to +0.253 | 1.430×10⁻³ | 0.155 | 0/415,364 | 28/64 | 7/8 |
| 4 | Exact preservation | −0.140 | +0.220 | −0.654 to +0.348 | 1.486×10⁻³ | 0.159 | 0/412,631 | 40/64 | 8/8 |
| 5 | Future forecast | −0.782 | −1.000 | −1.243 to −0.291 | 1.532×10⁻³ | 0.150 | 1/498,033 | 30/64 | 6/8 |
Negative log-likelihood by update
Improving the Policy at Test Time
The traces separated two problems that the aggregate score had mixed together. The policy needed its trained behavior to hold reliably across a campaign, and its forecasts needed a better empirical prior. Training improved action validity and short-horizon control, after which we held the weights, runtime, campaign environment, metric, and scoring code fixed to ask how far additional inference could push the same learned policy. Later setups used the full response format instead of the compressed action contract used by the first evaluation.
| Inference setup | Adaptive AUC | Behavioral result |
|---|---|---|
| Completion and behavior rules | −1.5101 | 12 of 12 branches completed; indicator rate fell to 4.6% |
| Experience-grounded forecasts and three-draw pooling | −1.4664 | 0 of 306 eligible rows triggered the indicator; endpoint +0.023 |
We translated recurring trace failures into seven behavior rules and added a separate completion rule that required the policy to use its full experiment budget. The tested setup also retained earlier instructions about evidence use.3 All 12 branches completed and the unreviewed-refinement overclaim indicator rate fell from 32.7% to 4.6%, while adaptive AUC remained effectively unchanged at −1.5101 compared with −1.5138 before the change. Behavior became more reliable without a material gain in forecast quality. Because the rules were applied together, the study cannot assign the result to any individual rule.
The Precursor Genome contains 1,035 recorded pairwise reactions, so outcomes involving the same precursors provide a direct analog for a new candidate. An offline comparison found that conditioning each candidate on those recorded outcomes reduced forecast loss by 0.105 nats per item, giving us a measured target for a simple instruction. For each candidate, begin with relevant precursor-sharing experience, then adjust for evidence specific to the current campaign.
Because one forecast still carried sampling variance, we averaged three independent draws and weighted them equally, reducing variance through pooling instead of best-of-n search.
Together, experience grounding and three-draw pooling moved adaptive AUC from −1.5101 to −1.4664 while completing 12 of 12 branches. No eligible scored belief row triggered the unreviewed-refinement overclaim indicator, with zero flags across 306 rows, and endpoint gain moved above zero to +0.023.
A separate campaign that did not inform the revisions showed the same direction of forecast improvement. The six scored roots were inspected between revisions, so this inference study remains a development result rather than a held-out confirmation.
Trace analysis indicated that the gain came from better initial forecasts, not in-campaign evidence assimilation.
Results
On byte-identical trained weights under the same vLLM runtime, added inference moved adaptive AUC from −1.5138 to −1.4664. The final system also scored −1.4664, compared with −1.8931 for the Qwen3.6-35B-A3B base row, a combined system difference of 0.4267. The base row used a pinned OpenRouter route, while the final system ran on our vLLM stack, so the wider comparison does not isolate training.
The comparison below places the follow-on rows beside the published SDL-1 systems. It is a descriptive comparison, not a controlled leaderboard.
| # | System | Adaptive AUC ↑ · zoom −1.95 to −1.0 | Mean | Selection lift | Endpoint gain |
|---|---|---|---|---|---|
| 01 | Claude Opus 4.8 | −1.2519 | plus 0.0086 | plus 0.0676 | |
| 02 | GPT-5.6 Sol | −1.2864 | plus 0.0563 | plus 0.0435 | |
| 03 | Grok 4.5 | −1.3345 | minus 0.0377 | minus 0.0578 | |
| 04 | Gemini 3.6 Flash | −1.4325 | plus 0.0060 | plus 0.0750 | |
| 05 | Ours (35B-A3B)follow-on | −1.4664 | plus 0.0091 | plus 0.0228 | |
| 06 | GLM 5.2 | −1.5280 | plus 0.1577* | plus 0.0569 | |
| 07 | Qwen3.6-35B-A3B (base)follow-on | −1.8931 | minus 0.1582 | plus 0.0339 | |
| 08 | DeepSeek V4 Flash† | off zoom scale | −6.7473 | Omitted | Omitted |
* GLM 5.2’s selection lift is driven by one root with a lift of +0.958.
† DeepSeek V4 Flash ran in a compute-limited configuration that averaged 365.5 output tokens per call. Poorly calibrated absolute forecasts make its published within-row selection and endpoint differences unsuitable for capability comparison, so those values are omitted here. This row describes only that compute-limited configuration.
The final system outperformed GLM 5.2, the strongest complete open-weight row in the original benchmark, by 0.0616. It finished 0.0339 behind Gemini 3.6 Flash, a gap below SDL-1’s minimum meaningful effect of 0.0488.
The published systems ran on their own runtimes, and 58 of the 192 canonical evaluation-tile rows appear in our gradient inventory through alternative-fold reuse. The potential weight-level exposure favors our row, so we make no untouched-benchmark claim.
| SDL-1 failure | Final result | Boundary |
|---|---|---|
| Claims exceeded the available evidence | 0 of 306 eligible scored belief rows triggered the unreviewed-refinement overclaim indicator; all 234 eligible belief-update actions passed first-pass validity | This removes the measured failure class, not every possible unsupported claim |
| Local updates failed to improve held-out forecasts | Not resolved; 0 of 468 later update turns incorporated acquired evidence into held-out forecasts | The post-hoc audit covered both evaluation branches; endpoint gain was +0.0228 because initial forecasts improved |
| Selection lift changed sign across assignments | Mean lift reached +0.0091 | The effect remains inside evaluation noise |
The final system remained active as the measured evidence discipline improved. It completed all 12 campaign branches, and mean local sample log-loss improvement per update rose from +0.059 to +0.082 as the unreviewed-refinement overclaim indicator rate fell from 32.7% to zero.
A post-hoc trace audit indicated that the endpoint gain came from forecasts made before the campaigns began. None of 468 later update turns across the adaptive and schedule-matched random branches incorporated newly acquired campaign evidence into their held-out forecasts.
The system entered each campaign with better forecasts grounded in recorded experience, but it did not reliably carry purchased evidence into later predictions.
The following cases were selected post-hoc from the final evaluation.
Waiting for sufficient evidence
- Status
- Post-hoc example from the final evaluation
- Selection rule
- Lowest post-review local loss after the policy withheld a claim, acquired expert review, and then updated.
- Audit scope
- Complete audited review sequences in the final evaluation.
Decide whether In₂O₃ and Y₂O₃ formed YInO₃ after heating at 1100 °C.
“So I must use
claim_scope: "evidence_insufficient"and preserve the full belief exactly.”
The policy submitted an empty belief update, requested expert review, and then updated only after the accepted review supported the phase interpretation. It moved target-phase probability from 0.30 to 0.05 and unreacted probability to 0.95.
Local joint log loss fell from 1.151 to 0.103. The complete root's held-out loss later worsened by 0.042.
Trace context
The policy had to decide whether In₂O₃ and Y₂O₃ formed YInO₃ after heating at 1100 °C. At the start of this sequence, it had seven experiment slots, 20 evidence units, and one expert review. The refinement cost one evidence unit and reported only the two precursor phases, but it had not been reviewed.
The policy could see the unreviewed refinement, its current belief, the remaining budget, and the available expert review. The recorded physical result remained outside its state.
It chose the less expensive evidence first.
“I haven't inspected the refinement or scan metadata yet. They are cheaper evidence types than expert review. So I should inspect the refinement first.”
After reading the refinement, it refused to turn the fit into a chemical claim.
“So I must use
claim_scope: "evidence_insufficient"and preserve the full belief exactly.”
The policy submitted an empty belief update, requested expert review, and then updated only after the accepted review supported the phase interpretation. It lowered the probability of the target phase from 0.30 to 0.05, raised the probability of an unreacted result to 0.95, and closed the experiment without buying scan metadata that it judged unnecessary.
The accepted review agreed with the recorded result. Only In₂O₃ and Y₂O₃ were present. The target YInO₃ phase had not formed.
This case had the lowest post-review local loss among the complete audited sequences in which the policy withheld a claim, acquired expert review, and then updated; local joint log loss fell from 1.151 to 0.103. The complete root's held-out loss later worsened by 0.042, so a correct local update did not guarantee transfer. The policy also assigned only 0.30 probability to the review changing its conclusion, although it did.
Better priors, incomplete assimilation
- Status
- Post-hoc example from the final evaluation
- Selection rule
- State A is the strongest matched-state improvement whose trace used recorded analogs. State B required acquired evidence in the state and a later forecast rationale that did not acknowledge it.
- Audit scope
- State A covers the audited matched-state shortlist. State B comes from the post-hoc audit of 468 later update turns across both evaluation branches.
Two separate evaluation roots show improved initial grounding and incomplete later transfer.
Improved initial grounding
Forecast the same recorded Cr₂O₃ and WO₃ experiment at 900 °C from the same panel of 32 queries and 96 recorded experiences.
“I should use the recorded experiences to estimate the distributions for each future experiment based on shared precursors.”
The base policy assigned 0.10 probability to the recorded unreacted outcome. The final system assigned 0.29.
Item loss fell from 2.3645 to 1.2892 and panel loss from 1.6542 to 1.5411.
Transfer remained incomplete
After an Fe₂O₃ and Na₂CO₃ experiment, forecast a held-out Co₃O₄ and Fe₂O₃ experiment that shared one precursor.
“Since this is a probe with no new evidence yet...”
The pooled forecast assigned 0.2633 probability to an unreacted result.
The recorded held-out outcome was unreacted. The item loss was 1.4213.
Trace context
These two traces come from separate evaluation roots. The first compares an initial forecast that ignored recorded experience with one that used it and scored better. The second shows that newly acquired campaign evidence could still disappear from a later policy trace.
Recorded trace · 02 · improved initial groundingThe Qwen3.6-35B-A3B base policy and the final system forecast the outcome of the same recorded Cr₂O₃ and WO₃ experiment at 900 °C. Both received the same panel of 32 queries and the same 96 recorded experiences.
Nineteen of those experiences shared Cr₂O₃ or WO₃ with the query. The base policy treated an empty acquisition history as an absence of prior evidence.
“Since this is the first turn and acquisition history is empty, I have no prior evidence.”
The final system instead cited the records already in context and used their approximate outcome frequencies.
“I should use the recorded experiences to estimate the distributions for each future experiment based on shared precursors.”
The base policy assigned 0.10 probability to the recorded unreacted outcome. The final system assigned 0.29.
The experiment was recorded as unreacted. This result was private to the evaluator when both forecasts were made.
Item loss fell from 2.3645 to 1.2892 and panel loss from 1.6542 to 1.5411, the strongest matched-state improvement in the audited shortlist whose policy trace explicitly used recorded analogs. It is a descriptive comparison because the base and final systems used different weights, prompts, inference methods, providers, and runtimes.
In a different campaign, the final system had completed an Fe₂O₃ and Na₂CO₃ experiment and then forecast a held-out Co₃O₄ and Fe₂O₃ experiment that shared one precursor.
The state contained seven acquired evidence items and a closed-campaign belief that assigned 0.85 probability to an unreacted result.
One forecast draw began this way.
“Since this is a probe with no new evidence yet...”
The pooled forecast assigned 0.2633 probability to an unreacted result.
The recorded held-out outcome was unreacted.
The item loss was 1.4213. The recorded rationale did not acknowledge evidence that was present in the state. It does not establish the probability the policy should have assigned, and we do not use the earlier forecast as a numerical baseline because the two forecasts used different ensemble sizes.
A post-hoc trace audit indicated that the endpoint gain came from forecasts made before the campaigns began. None of 468 later update turns across the adaptive and schedule-matched random branches incorporated newly acquired campaign evidence into their held-out forecasts. The endpoint gain was +0.0228 because initial forecasts improved.
Experiment selection without decision value
- Status
- Post-hoc example from the final evaluation
- Selection rule
- The only turn that combined an arbitrary choice, an evidence plan after both budgets reached zero, and a statement that those resources remained.
- Audit scope
- Every adaptive selection turn in the final evaluation.
Choose among 22 candidate experiments with two experiment slots left, no evidence budget, and no expert reviews.
“Actually, any valid experiment ID from the candidate list is fine as long as I follow the schema.”
The policy selected an experiment and planned to inspect execution, thermal history, diffraction, refinement, and expert review. None of those resources remained.
The action was valid and the campaign finished, but the rationale did not connect the experiment to available resources or expected decision value.
Trace context
Near the end of one campaign, the policy had two experiment slots left, no evidence budget, no expert reviews, and 22 candidate experiments. The ten completed experiments had already produced 39 evidence items.
Several candidates shared well-represented precursor families with the 96 recorded experiences. The policy narrowed the menu to three candidates, then stopped comparing their expected value.
“Actually, any valid experiment ID from the candidate list is fine as long as I follow the schema.”
The policy selected an experiment and described a plan to inspect execution, thermal history, diffraction, refinement, and expert review. None of those resources remained.
The environment returned an empty evidence catalog. The physical outcome remained private, so the policy could submit only a prior belief before closing the experiment.
The action was valid and the campaign finished, but the selection rationale did not connect the experiment to available resources or expected decision value. This is the clearest final-evaluation selection failure under a deterministic post-hoc rule applied across every adaptive selection turn.
It was the only turn that combined an arbitrary choice, an evidence plan after both evidence and review budgets reached zero, and a statement that those resources remained.
These post-hoc cases come from the final evaluation. The detailed trace context preserves the evaluator boundary, audit scope, and limits of each comparison. Quotes are verbatim from recorded policy traces.
The final system could wait for sufficient evidence and begin from better empirical priors. It could still lose acquired evidence between decisions and choose an experiment without establishing why it was worth the remaining budget.
The interaction between the policy and the campaign turns each failure into a measurable training target.
Limitations
The policy did not reliably carry newly acquired evidence into later forecasts. Its positive endpoint gain came from better forecasts before the campaigns began, not from in-campaign evidence assimilation.
Experiment selection also remains unresolved. Mean selection lift stayed inside evaluation noise, and the traces show that a valid experiment choice can still lack a clear connection to available resources or expected decision value.
SDL-1 begins after the objective and available experiments have been defined. It does not measure whether a policy can frame the right question, choose a research direction, or determine the best time to stop. These boundaries separate evidence-conditioned campaign control from complete scientific agency, and they define the decision axes that future environments must make measurable.
What’s Next
SDL-1 made past campaigns replayable. The next step is to make future campaigns compilable.
Future campaigns should begin with the decision to be made, current evidence, constraints, required proof, budget, and time. A campaign compiler can use that specification to compare experimental strategies across recorded experience, validated digital twins, and connected laboratories, then direct physical work toward the branch most likely to resolve the consequential uncertainty.
Each completed campaign preserves the path from intent through experiments, evidence, failures, and physical results to the decision it supported. Differences between predicted and observed behavior can sharpen the twins and verifiers, and decisions made along the way can become new training environments for the policy. A physical autoresearch system can use that record to allocate compute, instrument time, materials, and human attention toward the smallest campaign that produces the proof required to act.
SDL-1 shows that a completed experiment can train the policy that plans the next one. Connecting that loop to live campaigns would let every result improve both the engineering decision in front of the system and the scientific judgment applied to the next campaign.