How do you know a fine-tuned AI model is actually better?

You measure it. Hold out a portion of the client's real examples so the model never sees them during training, score the plain base model on those held-out questions first, fine-tune, then score again on the identical questions with identical scoring. The difference is the lift. Because the only thing that changed is the fine-tune, the improvement is attributable to it.

Does fine-tuning actually improve accuracy, or is the base model already good enough?

It depends on the task and, critically, on how much data you have. On a public benchmark of 510 lawyer-annotated commercial contracts, a base Qwen3-4B extracted short contract fields at 62.2% accuracy. Fine-tuned on 396 examples it reached 83.5-85.4%, a lift of 21.3 to 23.2 points across three runs. The same model trained on only 48 examples produced a lift inside the noise floor, so the amount of data was the deciding factor rather than the model's ceiling.

How much of our own data do we need to fine-tune a model?

Fewer examples than most people expect, but more than a handful. In our contract-extraction measurements, 48 training examples produced no measurable improvement while roughly 400 produced a 22-point gain. The honest answer for any specific case is that it depends on how varied and how consistent the examples are, which is what a paid readiness assessment measures on the client's own corpus.

Why can't you just use a public AI benchmark score?

Public benchmarks measure general ability on standardised tests, not your work. A model that scores well in the abstract can still be mediocre at reading your contracts or following your policies. Public benchmarks are also increasingly targeted during training, so a high score can reflect test preparation as much as capability. The only benchmark that answers your question is built from your own tasks.

Research record

At Width 96 It Holds

By Joshua Bolick, Awareness Software Group ~9 min read August 2026

Ongoing research. This is an experimental result from active work, not a settled conclusion. The numbers are what we measured and the method is described so you can judge it, but the programme is still running and later experiments may revise what it means.

A note on the language in these records. This is a working laboratory notebook for research into training AI models more cheaply and efficiently, so you will read that an approach did not work, that a result did not hold up, or that one method was worse than another. That is the research doing its job, not a verdict on the engineering we deliver to clients. Ruling an approach out is how the search narrows, and these are the pages that teach us the most: nearly every technique we now rely on came from understanding why something else fell short. Testing our own ideas at least as hard as anyone else's is the point of publishing them. More about this programme and why we run it.

Part of a bigger question: Is the task we are studying actually hard? – Often it is not. A rule from 1990 with no parameters beats the trained model on the task most of these results were measured on, and what an intervention costs is set by the task's own structure.

In plain English

What we asked. Our easy-sum speed-up had only been measured in one size of model. We tried a model twice as wide, on a hard sum chosen to challenge it about as much as the original sum challenged the smaller model.

What we found. The speed-up held at the same size: the typical run solved it in about 2,550 steps with the easy start against 4,475 without, about 46 percent fewer. Every run of both recipes got there, so this is the cleanest comparison of the whole study.

Why it matters. Two sizes of model is still a narrow range, but a result that survives doubling the model is worth more than one that has only been seen once.

The rest of this page is the technical record: the design, every number, and the limits. It is written for a reviewer, and you do not need it to have understood the result above.

New here? How to read a research record

Start at the verdict. Every record states, before the experiment was run, what result would have made us abandon the idea. That is the "kill test". Then it says whether the test fired. Nothing gets reinterpreted after the fact.
Numbers in square brackets are uncertainty. 23.4 [18.1, 28.7] means our best estimate is 23.4 and the true value is probably somewhere in that range. If a range includes zero, we cannot claim an effect.
Results that rule an idea out are kept. Roughly half of what is published here says an approach did not work, including plenty of our own. Those pages are the output, not a shortfall: knowing which direction is a dead end is what lets the next experiment go somewhere better, and most of what we now rely on came out of understanding why something else fell short. Work that only publishes what worked is not measuring anything.
Read the Limits section. Every record ends with what it does not show. It is the most honest part of any experiment and usually the shortest.
Pro tip: the figures near the top are designed to carry the result on their own. If you read nothing else, read the caption under each one, which says what it shows and what to take from it.

EXPLORATORY. Not a preregistered study. Local CPU, 32 training runs of 10000 steps at width 96 on sixteen fresh seeds. The design, the disclosed throwaways choosing the target and the kill test were committed (e518d28) before any run.

Program v2 Bucket A, item A53. Decisive computation: analysis/sum_mixture_wide.py. Output: analysis/sum_mixture_wide.json.

The question

Every modular-sum result so far is a width-48 GRU: the early mix of easier sums reaches the solution in about 40% fewer steps than the best plain recipe (A44). P11's rule: a width sweep must keep the task at the model's edge. Does the speed-up hold at width 96?

**In a model twice as wide, the easy-sum start is still about twice as fast.** A model twice as wide as before, on a hard sum chosen to sit at the edge of what it learns in the budget. Each line counts how many of sixteen runs have reached 90% by each step. *Every run of both recipes gets there; the easy-sum start gets there in about 2,550 steps against 4,475 -- about 46% fewer, the same size of saving as in the smaller model.*

Design: width 96; target (2, 6), chosen by throwaways as the pair width 96 solves near the end of the budget at rate 0.003 (as (2, 7) is for width 48); 10000 steps, sixteen fresh seeds. Mixed (2000 steps of (2,3)/(2,4)/(2,5), then (2, 6)) against plain with a 500-step learning-rate warm-up, both at 0.003. Endpoint: steps to 0.9. Kill test, fixed before execution: mixed minus plain includes zero or lies above it. Anchor, in code: at width 48 the loop reproduces A40 -- held.

Results

Arm (width `96`, sixteen fresh seeds)	Median steps to `0.9`	Solved by `10000`
easier sums mixed first	`2550`	`16`
plain, learning-rate warm-up	`4475`	`16`

Mixed minus plain: -2195.6 [-2795.2, -1596.0] steps. Ratio of mean steps 0.544.

The kill test does not fire. At twice the width, on a target matched to it, the mixture reaches the solution in about 46% fewer steps on average, and -- unlike every width-48 test -- every seed in both arms solves the task, so nothing here is censored. The interval is the tightest in the thread.

What it says

The speed-up is not a width-48 artefact: at width 96 it is the same size (ratio of means 0.544 against 0.578 at width 48) and cleaner. Two widths is still a narrow range, and the target had to change with the width, as P11 requires. (The throwaways also found width 96 solving (2, 7) less readily than width 48 at these rates -- noted in the pilot, not tested.)

What stands

A53: kill test does not fire. Width 96, (2, 6): mixed minus plain -2195.6 [-2795.2, -1596.0] steps; ratio of means 0.544; all sixteen seeds solve in both arms.

Limits

Sixteen seeds, one larger width, one target, 10000 steps (trimmed because width 96 is slow on this laptop).

Terms on this page

Every piece of vocabulary this record uses, in plain language. Generated from the text above, so it cannot drift out of step with it.

GRU: Gated Recurrent Unit. A compact design for processing sequences one item at a time, with internal switches controlling what it keeps in memory.
kill test: A condition written down before running the experiment that says what result would make us abandon the idea. Fixing it in advance is what stops a disappointing result being reinterpreted as an encouraging one.
learning rate: How big a step training takes each time it updates the model. Too small and nothing happens; too big and it never settles.
seed: The number that fixes all the randomness in a training run. Same seed, same run. Running several seeds is how you tell a real effect from a lucky one.
width: How many internal numbers a model uses at each layer. The usual way we vary model size in these experiments.