Prior or Feedback? What an LLM Uses When Adapting Neural Operators

AI summary

Overview

Research area: AI for science / LLM scientific agents applied to neural operator adaptation — specifically, verifying what an LLM-based search policy actually uses when it configures fine-tuning of a pretrained Fourier neural operator (FNO).

Technical level: Intermediate. The intervention protocol and distance metric are simple to follow, but the setting assumes familiarity with fine-tuning, hyperparameter search, neural operators, and PDE benchmarks.

Scope: A fixed-budget study of one hosted LLM policy (deepseek-v4-pro) adapting FNO checkpoints across twelve source–target PDE cells of 1D advection and Burgers' equations, with controlled input interventions to test whether the policy's decisions depend on the task description and on observed validation feedback.

What This Paper Is About

LLM agents for science propose actions, see results, and decide what to try next — but a final benchmark score cannot tell you which inputs shaped any individual decision. This paper asks whether an LLM search policy adapting a pretrained neural operator relies on a prior formed from the task description (the "cold start"), or whether it actually changes its proposals in response to experimental feedback.

The authors attack this by holding everything else fixed — the FNO checkpoint, the data, the action space, and the 20-trial budget — and intervening on one policy input at a time to read out how much the next proposed configuration moves.

Key Contributions

1. A matched, fixed-budget comparison. With the same 20-trial budget, the LLM policy reaches lower held-out test nRMSE than random search and than a Tree-structured Parzen Estimator (TPE), spanning within-family and cross-family transfer between advection and Burgers' PDEs.

2. A decision-level verification protocol. Instead of only measuring endpoints, the authors intervene on a single displayed input at a time — the PDE description at cold start, and the assignment of validation scores once a history exists — and report the resulting change as an action distance between proposed configurations over a 12-dimensional action space, rather than a binary "did it change" indicator.

3. Evidence of a task-dependent prior. Before any score is observed, the first LLM proposal already ranks near the top of the corresponding random-search pool, and switching the displayed PDE family doubles the median base learning rate in the first proposal.

4. Evidence of feedback sensitivity. Permuting which validation score belongs to which evaluated configuration changes the next proposal by about one categorical-coordinate change, while a value-preserving rewrite of the same scores does not.

Main Findings

• The LLM wins the fixed budget, but narrowly framed. Under the shared 20-trial budget the LLM found a configuration with lower held-out test nRMSE than random search in all 36 matched runs and than TPE in 35 of 36. All 12 cell medians favour the LLM. The authors stress this is a finite-budget advantage, not asymptotic superiority: TPE is still improving at trial 20 in several advection-to-Burgers' runs.

• The TPE startup allocation does not explain the ranking. A separate control restores Optuna's default ten TPE startup trials and extends TPE's budget to 25 evaluations so it keeps all fifteen model-based proposals. The LLM still records lower held-out test nRMSE in 5/6 comparisons and both cell medians. Median TPE-to-LLM ratios are 1.91x within-family and 2.50x cross-family. The single TPE win is on the same cell and seed as in the main comparison (TPE reaching 0.0248 here versus 0.0263 with five startup trials).

• A useful cold-start prior exists. Before observing any validation score, the median first LLM proposal has lower validation nRMSE than 91.7% of the 60 random-search configurations evaluated in the corresponding cell; only two of the 36 first proposals fall below their cell's random median. The median lower-tail quantile is 8.3%, 28 proposals beat at least 75% of their pool, and 34 beat at least half.

• The PDE description shifts the first proposal. Switching the displayed description from Burgers' to advection doubles the median base learning rate in the first proposal, from 0.0005 to 0.001, in both target cells. A one-sided Mann-Whitney test over the pooled proposals (90 per displayed description, 45 from each target cell; U = 5777.5 of 8100 pairs) gives p = 5.2 x 10^-9, with a tie-corrected normal approximation of p = 1.0 x 10^-8. The advection description selects 0.001 in 80% of proposals, against 39% under the Burgers' description and 40% with no description. The no-description median is 0.0005 in both cells. Averaged over all twelve coordinates, the aggregate action distance between descriptions is only +0.0025, about one thirtieth of a single categorical-coordinate change, with p = 0.015.

• Reassigning validation scores changes the next configuration. Reassignment increases the median trace effect by +0.085 relative to a notation control (bootstrap 95% interval [+0.073, +0.108]), close to the 1/12 = 0.083 contribution of one categorical-coordinate change. All 18 trace effects and all six cell medians are positive, exceeding the authors' 0.05 decision threshold with p = 0.015625. Cross-family reassignment versus resampling gives +0.083 at p = 0.015625.

• The effect is not formatting or sampling noise. The notation control preserves every score and its assignment while rewriting each score in equivalent scientific notation (for example 0.0129 as 1.29e-2). Its median effect is zero relative to identical-prompt resampling, with bootstrap 95% interval [-0.006, +0.005] and p = 0.63 — despite editing the prompt more heavily than reassignment does (character-level Levenshtein distance of 76–160 versus 22–95). A feedback-bundle control that permutes each score together with its own trial's diagnostics still shows a median action-distance gap of +0.080 within-family and +0.054 cross-family, with 18/18 positive traces and exact one-sided sign-flip p = 0.015625 in each.

• The feedback response is selective by coordinate. 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. Optimiser changes stay near the resampling rate (7.8% versus 6.3%). The authors apply no per-coordinate tests and treat this ranking as descriptive only.

• Zero-shot reference scale. 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 5–400x the worst of the three adapted policy medians in the same cell.

• Stated limits of the claims. The interventions show the LLM policy depends on the task description and observed scores. They do not explain why, do not establish that its decisions are rational or reflect physical understanding, and do not show that either dependence explains the endpoint advantage.

Methodology in Plain English

The setup is a small, bounded adaptation loop. A pretrained FNO is adapted to a shifted physical regime over exactly B = 20 sequential trials. At each trial, a policy picks one configuration from a fixed action space: optimiser, learning-rate schedule, base learning rate, four parameter-block multipliers, weight decay, rollout length, data loss, and two auxiliary physics-loss weights. That is 8 numeric and 4 categorical coordinates, giving the D = 12 in the distance metric. Model size and epochs are fixed across policies and excluded from the action space, so any performance difference comes from configuration choices alone.

Each trial starts from a fresh copy of the source checkpoint, trains on 750 trajectories for at most 100 epochs, and is scored by nRMSE on an autoregressive validation rollout against a fixed 350-trajectory validation split. After the 20-trial search, the configuration with the lowest validation nRMSE is evaluated once on a held-out test prefix consisting of the first 1,000 PDEBench trajectories — PDEBench's own test split, so the released checkpoints did not train on it.

Three policies compete under the same budget. Random search uses neither problem context nor previous outcomes. TPE models the observed configuration–score history (using five random startup trials rather than Optuna's default ten, leaving fifteen model-based proposals). The LLM receives the same history plus a natural-language PDE description and training diagnostics, samples S = 3 JSON configurations per trial, and executes the medoid — the sampled configuration with the smallest total distance to the others.

The verification idea is the paper's distinctive move. Rather than retraining anything, the authors intervene on one displayed input and re-generate the next proposal. At cold start, they show an advection description, a Burgers' description, or no description, and read the shift in the first proposal's base learning rate. Once a history exists, they replay a logged decision point, permute which validation score is assigned to which evaluated configuration, and measure how far the regenerated proposal moves from the logged one. Two controls anchor the interpretation: a notation control that changes the score's characters but not its value or assignment, and an identical-prompt resampling control that captures the model's own generation variance.

Distance is measured by a normalised action distance over the twelve coordinates: absolute rescaled differences for the eight numeric coordinates plus 0/1 mismatch indicators for the four categorical ones. A single categorical change contributes 1/12 ≈ 0.083, and the authors set a decision threshold of roughly 60% of one such change (0.05). Aggregation deliberately treats each of the 18 traces — not each replayed decision — as the independent unit, collapsing resamples, windows, seeds, and cells in turn so the exact one-sided sign-flip test over six cell medians has a minimum attainable p-value of 2^-6 = 1/64 = 0.015625.

The LLM was the hosted deepseek-v4-pro with thinking and JSON modes enabled at reasoning_effort=max; thinking mode ignores temperature and nucleus settings, so proposal diversity comes from the model's own non-determinism. The served model fingerprint recorded on every proposal was fp_9954b31ca7_prod0820_fp8_kvcache_20260402. Runs were executed across 3,420 completed policy decisions and 10,260 valid LLM-generated configurations, on 2g.20gb MIG slices (about one quarter of an NVIDIA A100 80GB PCIe GPU) on the Eureka2 cluster at the University of Surrey. Code is at github.com/julian-8897/budgeted-search-ai4science and run records are archived at doi:10.5281/zenodo.23213042.

Why This Matters

Impact on research. Standard LLM-agent evaluations report an endpoint score, which cannot distinguish an agent that genuinely uses the evidence it collects from one that happens to land in the same place. By returning the size of the change rather than an indicator that a change occurred, the protocol offers a lightweight way to audit decision-making in hosted models whose internals are unavailable. It also reframes the comparison narrative: recent matched comparisons have shown LLM advantages are not universal (early gains can reflect default configurations, and classical optimisers can outperform standalone LLM proposals), and no policy here starts from a default, so the result is specific to operator fine-tuning under a fixed budget. The paper's own framing is that the LLM approach puts the expertise in the loop rather than in the operator weights or generated code — the architecture and starting checkpoint never change, only how the operator adapts.

Real-world applications the setting reflects (target-regime data are costly to generate and only a limited number of fine-tuning attempts are feasible):

• Fine-tuning simulation surrogates when a new physical regime is reached and only a handful of expensive training runs can be afforded.
• Scientific and engineering settings where domain experts need to adapt a pretrained surrogate but lack the machine-learning expertise to configure a fine-tuning run.
• Autonomy checks for unattended experimental loops, where two agents may reach the same score even if only one uses the evidence it gathers.
• Any workflow where a pretrained operator must be adapted to a shifted regime without regenerating the large pretraining corpus.

Industry relevance. Fine-tuning budget, GPU time, and expert configuration effort are all direct costs. The paper's fixed-action-space design means the LLM is choosing among existing knobs, not proposing new architectures, which makes the approach easy to bolt onto an existing training pipeline. The decision-level audit is also a compliance-style tool: if an agent's recommendations must be trusted, being able to demonstrate that the recommendations depend on the task description and the observed results — and not merely on prompt formatting — is a concrete, checkable property.

Future Directions

1. Generalise the protocol beyond one model and two PDE families. The study is explicitly limited in scope to one LLM and two one-dimensional PDE families, and the authors call for applying the protocol across model families, scientific domains, higher-dimensional PDEs, and larger budgets to test whether these sensitivities generalise.

2. Link the sensitivities to outcomes. The interventions do not show that either dependence explains the endpoint advantage. An open question is whether policies that respond more strongly to feedback also select better solutions.

3. Explain rather than just detect the behaviour. The protocol establishes that the proposal responds to the description and to reassigned scores; it does not explain why, or whether the response is rational or reflects physical understanding.

4. Extend decision-level auditing as a standard practice. The protocol needs only logged decision points and a distance over the action space, so it can be applied to other hosted LLM agents — a direction the authors position alongside other decision-level checks of AI agents.

Target Audience

Researchers and practitioners working on LLM agents for science, automated machine learning, and hyperparameter optimisation; engineers who adapt pretrained scientific surrogates such as neural operators under tight compute or data budgets; and anyone responsible for evaluating or auditing autonomous experimental systems. The paper is most valuable to readers who care less about "does the agent score well" and more about "can we show the agent's decisions depend on the evidence it was given."

Authors’ abstract

Do LLM scientific agents rely only on their initial task context, or do they adapt their decisions in response to experimental feedback? We study this question in neural operator adaptation, where a large language model (LLM) selects fine-tuning configurations under a limited trial budget. Across transfers within and between partial differential equation (PDE) families, the LLM achieves lower held-out test nRMSE than random search and Bayesian optimisation in nearly every matched comparison. Endpoint performance alone cannot distinguish what happens, so we verify each attribution with controlled interventions. Before observing any validation score, the LLM's first configuration already ranks near the top of the corresponding random-search pool, indicating a useful initial bias. A complementary cold-start intervention shows that the selected base learning rate shifts with the PDE description. Once feedback becomes available, reassigning validation scores among evaluated configurations changes the next proposal in every case tested, whereas a value-preserving rewrite produces no comparable aggregate effect. These interventions establish that the LLM's decision-level actions respond to the given task and observed outcomes, showing that it combines a task-dependent prior with sensitivity to experimental feedback.