Does an LLM Use Its Prior or Feedback When Adapting Neural Operators?

A benchmark score hides what shaped each decision

A scientific agent runs a loop: propose a configuration, observe the outcome, decide what to try next. When the loop ends, a single held-out score says how well it did but not which inputs steered the individual choices. Two agents could reach the same endpoint while only one actually reads the evidence it collects.

This paper isolates that question in a bounded setting. A frozen large language model acts as the adaptation policy for a pretrained Fourier neural operator (FNO), an architecture that learns solution maps between function spaces. The target physical regime has shifted away from the pretraining distribution, so the operator must be fine-tuned. The LLM chooses each fine-tuning configuration but cannot touch the data, the action space, the trial budget, or the external evaluation protocol.

Each policy gets 20 trials. At every trial it selects the optimiser, schedule, base learning rate, parameter-block multipliers, weight decay, rollout length, data loss, and two auxiliary physics-loss weights; a fresh copy of the checkpoint is then fine-tuned and scored. Model size and epochs are fixed and excluded from the action space, so differences between policies come only from configuration choices. The authors call the preference the policy shows before any evaluation the cold-start prior, a term about policy behaviour rather than evidence that the model knows the underlying physics.

Three policies differ in what they are allowed to see

Random search conditions on neither the problem description nor previous outcomes. A Tree-structured Parzen Estimator (TPE), a Bayesian optimiser built for mixed categorical and continuous spaces, models the observed configuration–score history but sees no problem text. The LLM receives that same history plus a natural-language description of the target PDE and training diagnostics.

Because the three policies differ in proposal mechanism, computational cost, and available information at once, endpoint performance can show whether the LLM is competitive under the budget but cannot show which of its extra inputs mattered. That is why the paper pairs the comparison with interventions that change one input at a time while holding the FNO, data, budget, and action space fixed.

The test bed is twelve adaptation cells over two one-dimensional PDE families. Six within-family cells keep the equation and change a governing parameter: advection at β = 0.1 is adapted to β of 0.4, 1.0, and 4.0, and Burgers' at ν = 1.0 to ν of 0.1, 0.01, and 0.001. Three cross-family cells adapt the advection checkpoint to Burgers' targets and three reverse that transfer. Each cell is run with three seeds that resample the train–validation split, giving 36 traces.

The LLM reaches lower held-out error in nearly every match

After the 20-trial search, the configuration with the lowest validation nRMSE is evaluated once on a held-out test prefix. Normalised root mean squared error (nRMSE) is the error metric here, and the held-out test set is separate from the validation split used to pick the configuration.

Against random search the LLM records lower held-out test nRMSE in 36 of 36 run-level comparisons. Against TPE it wins 35 of 36, with a median error roughly 4.4 times lower. The single TPE win is one cell and seed, and it persists in a control that restores TPE's default of ten startup trials and extends TPE to 25 evaluations so it keeps all fifteen model-based proposals; there the LLM still records lower error in 5 of 6 comparisons and in both cell medians.

A zero-shot reference puts the scale in context: applying the source checkpoint to the target with no adaptation gives held-out test nRMSE between 0.12 and 1.24 across the twelve cells, about 5 to 400 times the worst of the three adapted policy medians in the same cell. All three policies recover most of the error the regime shift causes. The comparison is therefore about how well each does so within 20 trials, not about whether adaptation is needed at all.

The first proposal already beats most of the random pool

Endpoint performance alone cannot separate a useful starting bias from lucky sampling, so the authors look at where the very first configuration lands. For each first proposal they compute the share of the 60 pooled random-search validation configurations in the same cell that score below it, counting ties as half.

Across the 36 first proposals the median lower-tail quantile is 8.3%, equivalent to beating 91.7% of the pool. Twenty-eight proposals beat at least 75% of their pool and 34 beat at least half. This is a placement within the random-search validation distribution, not a held-out test benefit, so it measures the quality of the starting point rather than the final result.

The cold-start intervention tests where that starting point comes from. In the advection β = 4.0 and Burgers' ν = 0.001 cells, the policy is shown an advection description, a Burgers' description, or no description before its first trial, with 45 medoid proposals generated per cell and condition. The median base learning rate doubles in each cell individually, from 0.0005 to 0.001, when the displayed description changes. A one-sided Mann–Whitney test in the pre-specified direction gives p = 5.2 × 10⁻⁹ by exact enumeration over the four distinct learning rates, or p = 1.0 × 10⁻⁸ with the tie-corrected normal approximation.

Reassigning scores moves the next proposal

To test whether observed outcomes matter, the authors replay a logged decision point and regenerate only the next proposal, without continuing the search or rerunning any fine-tuning trial. The reassignment intervention keeps the evaluated configurations and the validation scores but permutes which score is attached to which configuration. A notation control instead preserves every score and its assignment while rewriting each value in scientific notation, for example 0.0129 as 1.29e−2.

Displacement is measured as an action distance over twelve coordinates: eight normalised numeric ones and four categorical ones. A change in one categorical coordinate contributes 1/12 ≈ 0.083, and the authors set a decision threshold at roughly 60% of that, 0.05. Reassignment raises the median trace effect by +0.085 relative to the notation control, with a bootstrap 95% interval of [+0.073, +0.108]. All 18 within-family trace effects and all six cell medians are positive, and an exact one-sided sign-flip test over the six cells gives p = 0.015625, the smallest value attainable with six units.

The notation control is centred at zero against identical-prompt resampling, with interval [−0.006, +0.005], even though it edits the prompt more heavily: its character-level Levenshtein distance is 76–160 against 22–95 for reassignment. The effect survives a feedback-bundle control that permutes each score together with its own trial's diagnostics, with a median gap of +0.080 within-family and +0.054 cross-family and 18 of 18 positive traces in each. The response is also selective: reassignment changes rollout length in 49.6% of proposals, data loss in 40.4%, and schedule in 25.9%, against 14.4%, 15.9%, and 14.1% under resampling, while optimiser changes stay near the resampling rate. The authors apply no per-coordinate test and read that ranking as descriptive.

Sensitivity is not the same as rationality

The interventions support a narrow claim: the policy's decisions depend on the task description and on the observed scores. They do not explain why it responds as it does, show that its choices are rational or reflect physical understanding, or establish that either dependence causes the endpoint advantage. The cold-start effect is also confined to one of twelve coordinates; averaged over all twelve, the aggregate action distance between descriptions is +0.0025, about one thirtieth of a single categorical-coordinate change, with p = 0.015 from a one-sided permutation test. That aggregate uses a different reference from the replay measurement, so its magnitude should not be compared with the replay effect.

Scope is limited to one LLM and two one-dimensional PDE families. The policy samples three JSON configurations per trial and executes the medoid, the one with the smallest total distance to the others; that rule limits the influence of a single atypical completion but cannot correct a bias shared by all three, so the behavioural claims concern the chosen configuration. The search trajectories also do not establish that any baseline has finished improving by trial 20.

Decision-level checks separate two agents with one score

The paper's practical priority is not a new operator architecture or a new pretraining recipe. It holds the checkpoint and the target data fixed and puts the expertise in the loop, letting the LLM configure each fine-tuning trial from a fixed action space. That matters when target-regime data, training runs, or the expertise to run them are scarce, which is the setting the 20-trial budget is meant to reflect.

The verification protocol needs only logged decision points and a distance over the action space, so it can be applied to hosted models whose internals are unavailable. Its value is diagnostic: in an unattended experimental loop, two agents may reach the same endpoint score even if only one uses the evidence it gathers. Here the evidence points to both channels operating, with the cold-start prior visible in the first proposal's placement and in the doubled base learning rate, and feedback sensitivity visible as a next-proposal shift of about one categorical coordinate concentrated in rollout length and data loss.

The comparison that should guide a reader is therefore between what the endpoint measures and what the interventions measure. The 36-of-36 and 35-of-36 held-out wins establish that the LLM policy is competitive under this budget; the +0.085 reassignment effect and the 0.0005-to-0.001 learning-rate shift establish that its decisions respond to the description and the scores. Neither result substitutes for the other, and the paper's own framing is that scientific agent verification needs both.

Sources used in this answer