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 the Gap Holds Steady

By Joshua Bolick, Awareness Software Group ~10 min read September 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. In a model twice as wide, the easy-task warm-up helped less than in the small one, but the gap was still growing when training stopped. Given more time, would it keep growing, as it had in the small model?

What we found. No. Over two and a half times as much training, both versions kept improving and the warm-up stayed about five points ahead, never pulling further away. In the small model the gap had grown to thirty points.

Why it matters. So the large benefit we found does not simply carry over to a bigger model. There is a catch, though: the bigger model also needed a slower learning rate, and the next test checks whether that, rather than size, is what made the difference.

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, 16 training runs of 15000 steps. The design and the kill test were committed (5de4562) before any run.

Program v2 Bucket A, item A24. Decisive computation: analysis/warmup_width_longer.py. Output: analysis/warmup_width_longer.json.

The question

A19 found the varied warm-up helps at width 96 on a lag-12 target by +0.051 at step 6000 -- a quarter of width 48's gain -- with both arms still climbing and the gap still opening. At width 48, a longer run widened the gap from +0.215 to +0.304 (A16). Is width 96's smaller gain an early reading?

**In the larger model the warm-up's lead stays small and steady.** The larger-model experiment run two and a half times longer. One version trains on the hard task throughout; the other spends its first 1,500 steps on a random mix of easier versions. Same compute. Both keep improving, and the warm-up stays about five points ahead the whole way. In the smaller model the gap kept widening; here it does not. Whether that is the size of the model or the slower learning rate it needed is the next test.

Design: A19's code, arms and seeds run to step 15000. Kill test, fixed before execution: shuffled minus fixed at step 15000 includes +0.051 or lies below it. Anchor, in code: the first 6000 steps of both arms reproduce A19 exactly -- held on all eight seeds.

Results

Lag-`12` accuracy (mean of 8)	Step `6000`	Step `10000`	Step `15000`
fixed lag `12`	`0.563`	`0.659`	`0.729`
shuffled early, then lag `12`	`0.614`	`0.713`	`0.769`
difference, paired	`+0.051` `[+0.011, +0.090]`	`+0.054` `[+0.016, +0.092]`	`+0.040` `[+0.000, +0.080]`
seeds higher with the warm-up	`6` of `8`	`7` of `8`	`7` of `8`

The kill test fires. From step 6000 to 15000 both arms gain about 0.16 and the gap stays near +0.05, ending at +0.040 with an interval touching zero. At width 96 the warm-up gives a steady lead of about five points, not a widening one. Width 48's gap grew from +0.215 to +0.304 over the same extension; this one did not grow.

What it says

The width-48 picture -- a warm-up that changes which solution training finds, and so raises the ceiling -- does not reproduce at width 96 on this design. Here the warm-up reads more like a small constant head start that the plain run has not closed by step 15000.

But A19 changed two things at once. To keep width 96 at the edge of learnability it moved the task (lag 12, length 32) and halved the learning rate (0.005, because width 96 collapsed at 0.01). The standing rule applies: one change can alter two things. A26 has since shown the warm-up works through an early window of training, and a window is measured in the optimiser's clock -- which the rate sets. So the smaller effect may belong to the width or to the rate. A29 separates them: width 48, A15's task, at rate 0.005.

What stands

A24: kill test fires. At width 96 the warm-up's lead holds near +0.05 from step 6000 to 15000 and does not open (+0.040 [+0.000, +0.080] at 15000, 7 of 8 seeds higher).
The width-48 ceiling result (A16) does not reproduce at width 96 on this design.

Limits

Width, task and rate all changed between width 48 and 96; A29 isolates the rate.
A19's warm-up was 1500 steps of lags 3/6/9; A23 and A25 since found a shorter warm-up of one nearby lag does as well at width 48, and neither has been tried at width 96.

ANSWERED 2026-09-28 by A29. The smaller gain at width 96 goes with the rate, not the width: at width 48 and rate 0.005 the warm-up gives -0.034 [-0.104, +0.035], because the plain run does far better there. Text and numbers above unchanged.

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.

accuracy: The fraction of answers a model gets right on questions it was not trained on.
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.