Bio Capability Evals

What the eval is actually measuring

The object of a bio capability eval is not knowledge in the abstract; it is marginal risk — the additional capability a model confers beyond a well-defined baseline. That framing has a precise consequence: every number is a difference, and a difference needs two arms. If you only measure how well a model answers biology questions, you have measured a biology exam, not a risk.

Formally, if C_m is a subject’s task performance with the model and C_0 is their performance with a baseline toolset (web search, textbooks, reference protocols), the quantity of interest is the uplift Δ = C_m − C_0. A model can post a high absolute score and near-zero uplift — if everything it supplies was one query away anyway. Conversely a modest absolute score can hide meaningful uplift if it removes a genuine bottleneck. This is why bio evals are designed as controlled comparisons from the first line, and why an eval that reports only C_m is answering the wrong question.

Knowledge probes vs task-based evals

Two eval shapes dominate, and they trade off cost against realism. Knowledge probes are structured questions — typically multiple-choice items over technical biology, of which the WMDP-bio benchmark is the best-known public example. They are cheap, automatically gradable, and reproducible: you get a single accuracy number and a tight confidence interval for almost no marginal cost.

Their weakness is construct validity. Answering isolated facts correctly is a weak proxy for assembling those facts into a coherent plan under real constraints. Task-based evals attack that gap: they pose an open-ended, multi-step objective and score the quality of the resulting work. These are far more faithful to the actual threat model — capability is about synthesis, not recall — but they are expensive, slow, and hard to grade consistently. The practical stance is to use probes as a cheap, high-sensitivity tripwire and reserve costly task-based studies for models that clear the probe threshold. The probe tells you whether to look harder; the task study tells you how much to worry.

The uplift study: baseline is the whole game

An uplift study is a between-subjects (or crossover) experiment. Participants attempt the same set of tasks; the control arm works with the baseline toolset and the treatment arm additionally has the model. The measured quantity is the difference in task success or plan quality between arms.

Everything hinges on choosing the baseline honestly. Set it too weak — say, forbid the control arm from using the internet at all — and you manufacture uplift that reflects your handicap, not the model. Set it realistically — unrestricted search, standard references, the time a motivated person would actually invest — and the uplift you measure is the counterfactual that matters. A second design choice is participant expertise: uplift for a domain novice and uplift for a trained specialist are different quantities, and a study must state which population it is estimating. The cleanest studies pre-register the baseline, the population, the tasks, and the scoring rubric before any data is collected, so the answer cannot be tuned after the fact.

Scoring open-ended work reproducibly

Once tasks are open-ended, ‘did they succeed?’ stops being binary. The standard answer is a rubric: the task is decomposed into explicit sub-steps or quality dimensions, each scored on a fixed scale by trained graders who are blind to which arm produced the response. Blinding is not optional — a grader who knows an answer came from the model will score it differently, and that bias flows straight into Δ.

Because human scoring is noisy, each item is rated by multiple graders and their agreement is quantified — commonly with Cohen’s κ or an intraclass correlation. Low agreement means the rubric is ambiguous, and any uplift estimate built on it is unreliable regardless of sample size. A useful discipline is to separate process scoring (did the plan clear each checkpoint on the critical path?) from a single outcome score, because a plan can be plausible-sounding yet fail at one load-bearing step. Aggregating sub-scores into one number is itself a modeling choice that the rubric must fix in advance.

The statistics of detecting uplift

Suppose task success is binary and you compare two proportions: control success rate p_0 and treatment rate p_1. The null hypothesis is p_1 = p_0 (no uplift); you want to detect a true difference of at least δ = p_1 − p_0. The relevant question before running anything is statistical power: given your sample size, what is the probability you would actually detect an uplift of that size if it were real?

For a two-proportion z-test at significance α and power 1 − β, the required sample size per arm is approximately:

n ≈ ( z_(α/2)·√(2 p̄(1−p̄))  +  z_β·√(p_0(1−p_0)+p_1(1−p_1)) )^2  /  δ^2

where  p̄ = (p_0 + p_1) / 2,   δ = p_1 − p_0

The single most important feature of that formula is δ^2 in the denominator: halving the effect size you want to detect roughly quadruples the sample you need. Small, subtle uplifts are enormously expensive to measure — which is exactly why underpowered bio evals are so easy to misread.

A worked power calculation

Put numbers to it. Say the baseline success rate is p_0 = 0.30 and you care about detecting an uplift to p_1 = 0.50, so δ = 0.20. Use the conventional α = 0.05 (two-sided, z_(α/2) = 1.96) and 80% power (z_β = 0.84).

p̄ = (0.30 + 0.50)/2 = 0.40
term_1 = 1.96 × √(2 × 0.40 × 0.60) = 1.96 × √0.48   = 1.96 × 0.6928 = 1.358
term_2 = 0.84 × √(0.30×0.70 + 0.50×0.50) = 0.84 × √0.46 = 0.84 × 0.6782 = 0.570
n ≈ (1.358 + 0.570)^2 / 0.20^2 = (1.928)^2 / 0.04 = 3.717 / 0.04 ≈ 93

So you need about 93 participants per arm, ~186 total, just to reliably catch a large 20-point swing. Now shrink the target to a still-worrying δ = 0.10 and the requirement balloons past 350 per arm. Recruiting hundreds of appropriately-screened, expert participants is brutally hard — which is why so many published capability comparisons simply cannot resolve the modest effects that matter most.

Why underpowered evals mislead in both directions

An underpowered study fails asymmetrically, and understanding how keeps you honest. A null result from a small study is nearly meaningless: ‘we found no significant uplift’ with n = 20 per arm is fully consistent with a real, dangerous uplift the study had no power to see. Absence of evidence is not evidence of absence — report the confidence interval, and if it spans everything from ‘no effect’ to ‘large effect,’ the study is silent, not reassuring.

The opposite error is subtler. When power is low, the significant results that do slip through are biased upward — only unusually large sample-fluke effects clear the threshold, so any ‘significant’ uplift from a tiny study overstates the truth (the winner’s-curse or type-M error). The remedy is unglamorous: compute required n before running, pre-register the analysis, and treat both a lonely significant result and an underpowered null with the same skepticism.