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

Real on One Task Only

By Joshua Bolick, Awareness Software Group ~11 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: What actually makes training cheaper? – One thing has worked: stopping part of the training early saved about 7% with no loss of quality. Everything else tested has been matched by a simpler or cheaper method -- and in two cases the clever method was only winning because it was quietly being given more.

In plain English

What we asked. Our last experiment turned up a possible free speed-up: holding one part of a small model still for the first few dozen steps of training seemed to make it learn a bit better. Free speed-ups deserve suspicion, so we tested it properly: on a second task, measured as steps to learn, and against the same freeze placed at a random time.

What we found. On the original task it was real: the model learned about 7% sooner. On the second task it did nothing at all. So it is a quirk of one task, not a trick to use, which is the same thing we found for another early-training effect a few weeks ago.

Why it matters. We also got something wrong, and it is worth showing. Our random-time comparison could only start after step 50, but the model finished learning around step 87, so almost every random freeze happened after the learning it was meant to be compared with. That comparison could never have shown anything. The conclusion does not depend on it, but the lesson does: a control can be quietly decided by how it was set up.

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, six seeds, two tasks. The design, kill test and anchor were committed (a5673a7) before any run.

Program v2 Bucket O, item O10. Decisive computation: analysis/early_gate_freeze.py. Output: analysis/early_gate_freeze.json. Reproduce with python analysis/early_gate_freeze.py (about twenty minutes on a throttled laptop CPU); --reuse re-derives every endpoint from the saved series.

The question

O4 froze each part of a GRU for one stretch of training and found an unplanned negative cell: holding the update gate still for the first fifty steps made the run better (-1.80 points of mean error for its hidden weights, -0.92 for its input weights). A free manoeuvre -- and this programme's rules say a free manoeuvre needs a random-time-matched arm (K2, J7), a second task (R1), and pricing in steps to a criterion rather than in mean error.

**Holding one part still early: a real speed-up on one task, none on another.** A small model with one of its gates held completely still for fifty steps, either at the very start of training or at a random later time, on two different tasks. Below zero means it learned sooner than without any freeze. On the first task an early freeze makes it learn about 7% sooner. On the second it does nothing. So it is a quirk of one task, not a trick to use. The random-time bars on task 1 are flat for a reason we got wrong in the design: most random windows fell after the model had already learned.

The manoeuvre: both of the update gate's weight blocks held completely still (O4's hard freeze) for steps 1-50. The random arm: the same freeze for fifty steps starting at a point drawn per seed, from an independent generator, between steps 51 and 351. Tasks: delayed-copy (the house task) and dispatch-copy-8lag, both under L7's published criterion.

Kill test, fixed before execution: on either task the early freeze is not faster than the control with an interval excluding zero, or the random freeze does as well.

Anchor, in code, passed exactly: the delayed-copy control reproduces O4's committed series.

Result: the kill test fires

Steps to L7's criterion, paired against each seed's control:

	`delayed-copy` (control `86.7`)	`dispatch-copy-8lag` (control `169.2`)
early freeze minus control	`-5.8` `[-8.0, -3.7]`	`+4.2` `[-2.8, +11.1]`
random freeze minus control	`+0.0` `[+0.0, +0.0]`	`+0.8` `[-1.3, +3.0]`
early minus random	`-5.8` `[-8.0, -3.7]`	`+3.3` `[-3.8, +10.5]`

On the house task the early freeze is real: the model reaches the criterion 5.8 steps sooner, about 7% of its time to learn, with an interval clear of zero. On the second task it does nothing, if anything the opposite. The kill test fires on the second task, and the manoeuvre is a delayed-copy fact -- the same pattern L7 found for the critical period, and a fresh entry for R1's list of single-task results.

The random control was built wrong, and it is worth saying how

The random arm reads exactly +0.0 on delayed-copy, and that is my design, not the data. I drew the random window from steps 51-351 so that it could not overlap the early window. But the house task is learned by about step 87, so almost every random window started after the event it is timed against, and a freeze that starts after a model has learned cannot change when it learned. The contrast "early minus random" was therefore decided before the run: it could only equal "early minus control".

The control that would answer the real question -- is it the early window, or any fifty-step freeze before the transition? -- draws its window from before the event: for example, starts between 1 and 40, so every window overlaps the approach to the transition. This record does not have it, and its delayed-copy result therefore shows that the early freeze helps, not that the early window is special.

This is exactly the fault R14 audited the archive for -- a design parameter that decides its own answer -- and the audit found none in 138 committed pilots. It turned up here, in a fresh design, a day later, which is where R15 and R14 both said it would. The kill test's verdict does not depend on it: the manoeuvre fails on the second task regardless.

What stands

The kill test fires. The early update-gate freeze helps on delayed-copy (-5.8 steps, about 7%) and does nothing on dispatch-copy-8lag (+4.2 [-2.8, +11.1]).
It is a single-task effect, like the critical period, and not a manoeuvre to use.
The random-time control was inert by construction on the house task and does not establish that the early window specifically matters. Named here rather than repaired, because the verdict stands without it.

Limits

Two tasks, six seeds, one width. A task whose transition is as early as delayed-copy's might show the gain; dispatch-copy-8lag learns twice as slowly and may simply need its early update-gate movement.
One window length and one gate. O4's map suggested the update gate and the biases; only the gate weights were frozen here.
The control flaw above.

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.

critical period: A stretch of time during which something has to happen for development to proceed normally. Borrowed from biology, where it describes windows in which a young brain must receive certain input.
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.
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.