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

Kept In, They Get in the Way

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. Keeping easy sums in the training mix all the way through had stopped a small model learning a hard sum, but in that test the hard sum was only a quarter of the data. Was it just seeing too little of the hard sum?

What we found. No. With the hard sum three quarters of the data, as much as the model sees when the easy sums come first, keeping them in still stopped every one of 16 runs learning it. Plain training with no easy sums managed 5; easy sums as a short opening phase, 11.

Why it matters. Easy practice helps at the start and gets in the way later. When it happens matters, not how much of the real task the model sees.

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, 48 training runs of 8000 steps on sixteen fresh seeds. The design and the kill test were committed (0838673) before any run.

Program v2 Bucket A, item A50. Decisive computation: analysis/sum_mixture_dominant.py. Output: analysis/sum_mixture_dominant.json.

The question

A48 found that keeping easy sums mixed in with the hard sum (2, 7) for the whole run leaves every seed at chance, while the same sums as an early phase solve thirteen of sixteen -- but its throughout arm saw the hard sum only a quarter of the time. With the hard sum's exposure matched, does the early phase still win?

**Kept in the mix, easy sums get in the way even when the hard sum dominates.** Three recipes that see about the same amount of the hard sum: easy sums as an early phase; easy sums mixed in throughout with the hard sum three quarters of the data; and no easy sums at all. *As an early phase, easy sums help most. Kept in, they do worse than no easy sums at all: no run learns the hard sum. It is the timing, not how much of the hard sum the model sees.*

Design: A18's task at 0.003, 8000 steps, sixteen fresh seeds 18001-18016. Early: A40's arm. Throughout, hard-dominant: every step draws (2, 7) with probability 3/4, one of (2,3)/(2,4)/(2,5) otherwise -- about 6000 hard-sum steps, as the early arm has. Plain: a 500-step learning-rate warm-up. Endpoint: steps to 0.9 (never = 8000). Kill test, fixed before execution: early minus throughout includes zero or lies above it. Anchor, in code: the early arm reproduces A40's mixed run on its first seed -- held.

Results

Arm (sixteen fresh seeds)	Median steps to `0.9`	Solved by `8000`
early phase, then the hard sum	`3650`	`11`
easy sums kept in, hard sum `3/4` of the data	`8000` (budget)	`0`
plain, learning-rate warm-up	`8000` (budget)	`5`

Paired difference in steps to solve
early minus throughout	`-2939.4` `[-4168.8, -1710.0]`
early minus plain	`-2446.9` `[-3532.6, -1361.2]`
throughout minus plain	`+492.5` `[+23.1, +961.9]`

The kill test does not fire. With the hard sum seen as often as in the early arm, keeping easy sums in throughout still solves the task on no seed -- fewer than the plain run, which sees no easy sums at all and solves five. The interval against plain lies above zero (slower), and it understates the gap, since both are censored at the budget.

What it says

A48's confound is resolved: it is not under-exposure. Easy sums help as an early phase and actively get in the way when kept in. With A39 and A41 -- two of the easy pairs, trained on at length, delay learning of the target by thousands of steps -- the picture is of easy material that is useful for laying down the operation and a shared component early, and a distraction once the model needs to commit to the target's specific combination. That is the opposite of what arXiv 2410.03569's throughout-mixing did for its (much larger, differently structured) problem, and the same as the copy task's A17.

What stands

A50: kill test does not fire. Early minus throughout, exposure matched: -2939.4 [-4168.8, -1710.0] steps; solved 11 against 0.
Easy sums kept in are worse than none (+492.5 [+23.1, +961.9] steps against the plain run; 0 against 5 solved).

Limits

One mixing proportion (3/4), sixteen seeds, one budget that censors two of three arms.

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.

confound: A second explanation you did not control for. If bigger models both learn faster and score higher, then 'fast learners score higher' may be entirely about size and not about speed.
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.