Small Foundation Models of Human Cognition and Behaviour

AI summary

Overview

• Research area: Cognitive science and machine learning — specifically, fine-tuning large language models on human behavioural data to serve as general-purpose "cognitive proxies." Builds directly on the Centaur paradigm (Binz et al., 2025).
• Technical level: Intermediate. Familiarity with supervised fine-tuning, LoRA adapters, and negative log-likelihood helps, but the core arguments are accessible without deep ML background.
• Scope: The paper trains fourteen small models (135M to 14B parameters) on the Psych-101 dataset and uses ablation and permutation diagnostics to ask two questions — how much model scale actually matters, and whether these models process task structure or exploit statistical shortcuts.

What This Paper Is About

Centaur-style models fine-tune large language models on Psych-101, a dataset of 10.7 million trial-level choices from over 60,000 participants across 160 psychological experiments, and have been proposed as general-purpose proxies for human cognition. The prevailing approach used Llama-3.1-70B, leaving open whether 70 billion parameters are genuinely necessary and whether these models learn task structure or merely latch onto statistical regularities in choice sequences. Oh and Gobet address both questions by training fourteen much smaller models, varying scale, adapter capacity and training-set size independently, and then systematically stripping information channels out of the prompts to see what the models actually rely on.

Key Contributions

1. A scale sweep across four architecture families. Fourteen base (non-instruct) models from 135M to 14B parameters are fine-tuned on Psych-101: five Qwen3-Base models (0.6B, 1.7B, 4B, 8B, 14B), three Llama-3 models (1B, 3B, 8B), four SmolLM models (SmolLM2 at 135M, 360M and 1.7B; SmolLM3 at 3B), and two OLMo models (OLMo-2 at 1B, OLMo-3 at 7B). The fine-tuned variants are named Qwentaur, Llama-Centaur, Smoltaur and Olmotaur.

2. Independent variation of scale, adapter rank and data quantity. LoRA rank is swept over r ∈ {4, 8, 16, 32, 64} at full data, and training-set size is varied over nested, experiment-stratified subsets (1/16, 1/8, 1/4, 1/2, and the full set) at fixed rank r = 16, so each factor is isolated while the other two are held constant.

3. A four-channel decomposition of the prompt. The paper separates the prompt into task instruction (I), experimental stimuli (S), outcome feedback (F) and choice history (C), replacing the coarser formulation P(C_{t+1} | C_{1:t}, T) used in prior work. This permits a precise statement and test of the "shortcut hypothesis" in both its strong form (history sufficiency) and a weaker form the authors call format sufficiency.

4. Structural ablation and order-permutation diagnostics. Four ablation conditions (original, instruction-ablated, content-masked, history-only) are evaluated across 32 experiments, alongside order permutation tests on two experiments selected to anchor opposite ends of the exchangeability spectrum.

Main Findings

• Fine-tuning matters roughly ten times more than scale in-distribution. Qwen3-0.6B scores 0.731 before fine-tuning and 0.528 after, a gain of 0.203 nats; across the eight models the average gain is 0.188 (range 0.138 to 0.295). By contrast, going from Qwentaur-0.6B to Qwentaur-14B gains only 0.019 nats, and from Llama-Centaur-1B to Llama-Centaur-8B only 0.024 nats.

• The fine-tuning gain shrinks as base models grow. It falls from 0.203 at Qwentaur-0.6B to 0.138 at Qwentaur-14B, and from 0.295 at Llama-Centaur-1B to 0.158 at Llama-Centaur-8B. Larger base models already predict Psych-101 better, leaving less for fine-tuning to supply.

• Three to eight billion parameters suffice to match a 70B model. At rank 8 — the adapter capacity Centaur itself used (QLoRA, 4-bit base weights) — four models match or beat the authors' Centaur-70B reproduction (0.524): Qwentaur-8B and Llama-Centaur-8B (both 0.517), Qwentaur-4B (0.520) and Smoltaur-3B (0.523), with Qwentaur-1.7B close behind (0.528).

• Adapter capacity substitutes for parameters. Qwentaur-0.6B at r=64 (0.513) matches Qwentaur-14B at r=4 (0.516) with twenty-three times fewer parameters, and Llama-Centaur-1B at r=64 (0.520) matches Llama-Centaur-8B at r=4 (0.521) with eight times fewer. The size needed to match Centaur-70B moves from 8B at r=4 to 3B at r=8, 1.7B at r=16, and 0.6B at r=32 and above.

• Data returns diminish. Across nested subsets of Psych-101, Qwentaur-14B gains 0.016, 0.013, 0.009 and 0.008 nats over successive doublings. These are returns to depth (more participants per experiment); the return to breadth is unmeasured because all 160 experiments are represented at every subset size.

• In-distribution the models cluster; out-of-distribution they spread. At rank 16 on the full dataset, the eight matched models span just 0.028 nats on Psych-101 (from 0.509 to 0.537), a band that also contains the Centaur-70B reproduction. On the eighteen held-out experiments of Psych-201-RT they run from 0.788 to 1.033, a spread of 0.244.

• Scale buys transfer, not fit. Before fine-tuning, a tenfold larger Qwen3 predicts Psych-101 0.062 nats better and Psych-201 0.118 better; for Llama-3 the figures are 0.177 and 0.204. After fine-tuning, the in-distribution advantage nearly disappears (0.014 and 0.026) while the out-of-distribution advantage largely persists (0.104 and 0.172).

• All fourteen fine-tuned models beat the best base model in-distribution. That base model is an un-fine-tuned Qwen3-14B at 0.647. Out of distribution, only three do, against the same model at 0.869.

• Masking stimulus and feedback content destroys most of the learned information. Mean information retention R falls from original (1.00) to instruction-ablated (0.84), content-masked (−0.12) and history-only (−0.26). Each drop is significant (Friedman χ²(3) = 63.76, p = 9.3 × 10⁻¹⁴; pairwise Wilcoxon p < 2 × 10⁻³ throughout) and holds for all eight models.

• The loss partitions unequally across channels. The instruction accounts for 12.5% of the total loss, the content of stimuli and feedback for 75.7%, and the trial template for the remaining 11.7%. Neither form of the shortcut hypothesis survives — history alone does not suffice, and neither does the format.

• Most tasks degrade monotonically. 18 of 27 tasks (67%) degrade strictly monotonically across the four conditions. Of the nine exceptions, five invert only between two conditions that are already at or below chance, and four are genuine reversals.

• Order sensitivity tracks task structure. On THINGS odd-one-out (768 participants, exchangeable by construction), fine-tuned models cluster near zero variance, showing they learned the exchangeability of independent similarity judgements. On intertemporal choice (1,295 participants, an adaptive staircase), fine-tuned models are order-sensitive, as the design requires.

Methodology in Plain English

The authors take Psych-101 — a publicly released corpus of 10.7 million trial-level choices from over 60,000 participants in 160 psychological experiments, transcribed into natural language — and reuse Centaur's exact train–test splits and prompt templates. Each prompt encodes one participant's full trial-by-trial session.

They fine-tune fourteen pre-trained base (non-instruct) models using supervised fine-tuning with cross-entropy loss masked to human response tokens only, so the model is never optimised on the instructions or context itself. Adaptation uses rank-stabilised LoRA applied to all linear layers, trained for one epoch with AdamW (learning rate 5 × 10⁻⁵, weight decay 0.01) and a linear warmup of 100 steps, in bf16 on a single NVIDIA A100 80GB GPU. Training times range from 3 to 49 hours.

To isolate what drives accuracy, they vary three levers independently: model size, adapter rank (4 to 64), and training-set size (five nested, experiment-stratified fractions from 1/16 to the full set). They evaluate on Psych-101 for in-distribution prediction and on Psych-201-RT, a subset of Psych-201, for out-of-distribution transfer. Reported figures are mean negative log-likelihood in nats over the 38 of 46 Psych-101 tasks for which a domain-specific cognitive model is published.

The diagnostic half of the paper works differently. The prompt is split into four information channels — instruction, stimuli, feedback and choice history — and four ablation conditions are built. The key new condition is content-masked: stimulus values and feedback outcomes are replaced with generic placeholders ("some points", "a shape") and the instruction is reduced to a minimal action-space definition, while keeping each trial's formatting intact. This separates what the statements say from where the statements sit, which earlier instruction-ablation and choice-only tests could not do. Finally, order permutation is applied to two experiments chosen as opposites: THINGS odd-one-out, where trials are independent and order should not matter, and intertemporal choice, where each offer depends on the previous response and order should matter. For each participant–target-trial pair, 50 random permutations of the context are drawn and the variance of the response-token probability is measured.

Why This Matters

The paper reframes what these models are for. They are not theories of cognition in the tradition of ACT-R, CHREST or Soar — they posit no architecture and commit to no mechanism. What they offer is an estimate of the noise ceiling: an empirical bound on how much behaviour in a paradigm is predictable at all, and therefore how much room a process-level theory of that paradigm still has to improve. Used this way, a model returns not just a number but a map of where an interpretable theory falls short — the logic Agrawal et al. (2020) call scientific regret minimisation. Crucially, the ablations establish that the models reach this bound by using the information the experiment actually provides, which is what licenses treating them as instruments rather than as shortcut exploiters.

• Cheap noise-ceiling estimation for labs. Researchers running psychological experiments can get a predictability bound from a 0.6B to 8B model rather than a 70B one, within the paradigms represented in training.

• Benchmarking interpretable cognitive theories. Per-datapoint gaps between a noise-ceiling model and a handcrafted theory identify precisely where theory-building has the most to gain.

• Scaling decisions in behavioural-model deployment. Because scale buys transfer rather than in-distribution fit, teams can size models to how far beyond their training paradigms they need to generalise.

• Auditing claims about AI behavioural proxies. The four-channel ablation provides a reusable protocol for testing whether other behavioural models rely on real content or on template regularities.

Industry relevance: The released LoRA adapters and training code (github.com/socius-org/Centauri; hf.co/collections/socius/centauri) lower the compute barrier for building behavioural proxies, which matters for applied work in behavioural economics, survey research, and user-modelling. The paper also flags a risk the authors cite from D'Alessandro and Thompson (2025): widespread reliance on cheap AI-generated behavioural data could induce a "street light effect" in the cognitive sciences, with researchers gravitating toward questions these models can handle and neglecting phenomena that resist efficient simulation.

Future Directions

• Vary data breadth rather than depth. The subsets here are stratified so all 160 experiments contribute at every fraction, which holds paradigm coverage fixed by construction. Subsetting by experiment instead of by participant would estimate how many distinct paradigms a cognitive foundation model actually needs. Psych-201, at 3.5 times the size of Psych-101, is a step in that direction but does not escape the structural limitation.

• Collect cross-task participant data. Participants are nested within experiments in both Psych-101 and Psych-201, so no individual is observed across tasks. This precludes the cross-experiment person–task decomposition that Gobet and Ritter (2000) and Orr et al. (2025) identify as necessary for bounding predictability.

• Test whether full fine-tuning or other architectures shift the plateau. All adaptation here is low-rank; the rank sweep does not reveal where either the rank or the parameter axis ends. All four families are dense decoder-only transformers, leaving open whether the plateau moves under mixture-of-experts, state-space or hybrid designs. Supervised fine-tuning also optimises for imitation of the training distribution at a measurable cost to capabilities distant from it.

• Pair reinforcement learning with cross-task datasets. Kolluri et al. (2025) show contrastive DPO improves individual response accuracy over SFT, and Zhu et al. (2025b) find GRPO elicits chain-of-thought reasoning that improves choice prediction. RL is unlikely to surface novel cognitive mechanisms, since it redistributes probability mass over behaviours already in the pre-trained weights, but it generalises where SFT memorises — the regime the Psych-201 results identify as harder.

Target Audience

Cognitive scientists and psychologists looking for a data-driven noise ceiling against which to benchmark interpretable models of decision-making, memory, learning and planning. Computational cognitive modellers evaluating whether LLM-based proxies can replace or complement handcrafted architectures. Machine learning researchers interested in scaling behaviour, fine-tuning efficiency, and adapter-capacity trade-offs. Also relevant to behavioural economists and social scientists extending this paradigm to surveys, economic games and behavioural prediction, and to anyone assessing whether LLM behavioural proxies are trustworthy instruments or merely sophisticated shortcut learners.

Authors’ abstract

Large language models fine-tuned on human behavioural data have emerged as general-purpose cognitive proxies, but the scale this requires, and whether these models process task structure or exploit statistical shortcuts, remain open questions. We train fourteen models from 135M to 14B parameters across four architecture families on Psych-101, a dataset of 10.7 million trial-level choices from 160 experiments. In-distribution, scale barely matters. The models fall within a narrow band, as though against a ceiling, and 0.6B to 1B parameters suffice to match a 70B baseline on held-out participants. Out-of-distribution, that band opens into a markedly steeper scaling gradient, with larger models clearly advantaged in generalisation to novel task structure. To determine what information these models use, we run two diagnostics. We progressively strip four prompt channels -- task instructions, experimental stimuli, outcome feedback, and choice history -- across 27 experiments, and permute trial order. Masking the content of stimuli and feedback destroys 75.7% of learned information and pushes models below chance, demonstrating that choice history alone does not account for performance. Permutation reveals invariance on tasks with independent trials but sensitivity where trial order is determined by prior responses. Small cognitively fine-tuned models therefore show promise as noise ceiling estimators for psychological experiments, though their scope remains bounded by the paradigms seen in training.