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

A Five Second Check

By Joshua Bolick, Awareness Software Group ~12 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. One of our results said that reusing a finished model to give a new one a head start pays for itself after about five uses. A later result said some finished models are actively harmful to reuse, and that one quick test tells you which. Nobody had put those two next to each other, and doing so needed no new experiments at all: the data was already sitting in a file from the second one.

What we found. Put together, they change the picture rather than refine it. If you take a finished model without checking it first, you are on average worse off than starting from scratch. It costs you time rather than saving it. Run the quick check first and pick the best candidate, and it saves a substantial amount. The check is not a refinement on top of a good idea. It is the thing that makes the idea worth doing at all.

Why it matters. Two honest notes. The pool of candidates here is small, four kinds of task, so this shows the effect exists rather than mapping how it grows. And one of the four tasks is a case where nothing helps, so checking cannot help either; we left it in the averages rather than removing the one row that makes the method look worse after seeing that it does.

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. No new training. Re-analyses committed output.

Program v2 Bucket R, item R2. Decisive computation: analysis/donor_screening_economics.py. Output: analysis/donor_screening_economics.json. Reproduce with python analysis/donor_screening_economics.py; it reads analysis/relatedness_predicts_transfer.json and runs in under a second.

The question

P8 priced the transfer thread at 4.8 receivers per donor: train a donor once, hand it to enough receivers, and it pays for itself. That number assumes you already have a good donor.

**Choosing what to borrow from beats borrowing at random, by a wide margin.** A model that has finished one task can be copied into a fresh model learning another, and it either helps or hurts depending on which one you pick. Here we compare two ways of picking from the same set of candidates: taking one without looking, and running each candidate once on the new task first and taking the best. The model's own task is excluded from the candidates, so neither strategy can simply pick the obvious answer. The four tasks are: copy a token from a fixed distance back; the same but the distance is announced each time; the same with some labels randomised; and keeping a running count. Taking one without looking is worse than using nothing at all: it costs about twelve steps on average. Checking first turns that into a saving of about seventeen. So the check is not an optimisation on top of a good idea, it is the thing that makes the idea worth doing. The last pair is the exception and is left in deliberately: on that task nothing helps, so checking cannot help either.

Q14 then found that some donors are catastrophic, costing a receiver +85.7% of its own time to the transition, and that one forward pass separates the helpful from the harmful with a gap of 0.232 and nothing in it.

Those two have never met, and Q14's committed matrix already contains everything needed to introduce them. No new runs.

Kill test, fixed before execution: picking the best-scoring donor from a pool of k is no better than picking one at random from the same pool.

Prior recorded in advance: good that the screen wins, because Q14's separation was clean. The open question was whether picking at random is merely worse or actually negative. It is negative, which is the more interesting answer.

Result: the screen does not improve the economics, it creates them

Expected change in steps against a receiver given nothing. Negative is faster. The receiver's own task family is removed from the pool before either strategy chooses, because otherwise the screen trivially picks the same-task donor and the comparison is circular.

Receiver	pick at random	pick the best-scoring
`delayed-copy`	`+2.8` `[-1.7, +7.3]`	`-34.2` `[-39.3, -29.0]`
`dispatch-copy-8lag`	`+24.7` `[+16.5, +33.0]`	`-14.2` `[-21.1, -7.2]`
`noisy-copy`	`-0.0` `[-5.6, +5.6]`	`-40.0` `[-45.7, -34.3]`
`running-count`	`+20.8` `[+16.3, +25.4]`	`+20.8` `[+16.9, +24.8]`
all receivers	`+12.1` `[+6.8, +17.3]`	`-16.9` `[-27.5, -6.3]`

Screening minus random, paired within run: -29.0 [-36.5, -21.4] steps. The kill test does not fire.

A donor drawn without looking costs +12.1 steps, with the interval clear of zero. It is worse than no donor at all. So P8's 4.8 is not a number that screening improves: without screening there is no break-even to reach, because the donor never pays back at any receiver count. The screen does not make a good deal better. It is what makes there be a deal.

The row where screening does nothing, and why it is here

running-count reads +20.8 under both strategies, identically. The screen cannot help when every option is equally bad, and for that receiver they are: Q14 found all four of its arms within 0.8 steps of each other, because its control transitions at 37.5 steps while the graft lands at 30, so the row measures graft disruption rather than anything about donors.

It is left in rather than dropped. Removing the one row where a method does nothing, after seeing that it does nothing, is how a result gets better than it is. The pooled figures above include it, and the three interpretable receivers are stronger without it.

The circularity, measured rather than asserted

With the receiver's own task left in the pool, the screen picks it and the numbers look better: -27.9 [-40.7, -15.1] against random's +2.1. That comparison is close to arithmetic, since a model trained on exactly this task scores highest on exactly this task by construction.

Both are computed and both are in the output. The leave-one-out figures are the ones quoted, and they are the weaker of the two, which is the direction an honest choice should move a headline.

What stands

Picking a donor at random from a pool is worse than using no donor, +12.1 [+6.8, +17.3] steps.
Picking by a one-forward-pass screen saves -16.9 [-27.5, -6.3], a paired improvement of -29.0 steps.
The screen creates the break-even rather than improving it. P8's 4.8 receivers presumes a donor already known to be good; nothing in P8 said how you would know.
This is the first result in the transfer thread that is about a decision rather than a mechanism, and it cost no compute at all.

Limits

A pool of four task families, three after leave-one-out. This is an existence result, not a curve. How the advantage scales with pool size is untested and is the obvious next question.
It inherits every limit of Q14, including one width, one learning rate, one graft step, and the running-count row's contamination.
The screen is not free in the way "one forward pass" suggests, if the donors do not exist yet. This prices choosing among donors you have, not acquiring them. P8 priced the acquisition.
No new training means no new evidence. Everything here was already implied by Q14's matrix; what was missing was somebody putting it next to P8. That is worth doing and it is not the same as an independent confirmation.
Random pick is computed as the expectation over the pool, not as a simulated draw, so there is no sampling noise on top of the effect. That makes the comparison tighter than a real single draw would be, and a real draw is what a practitioner faces.

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.

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.
leave-one-out: A way of testing a rule fitted to data: leave one measurement out, fit the rule on the rest, and see how well it predicts the one you held back. It stops a rule from being graded on the data it was built from.
width: How many internal numbers a model uses at each layer. The usual way we vary model size in these experiments.