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

Only as Good as Its Forecast

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. There is a short sensitive moment just before a model learns its task. Until now we found it by watching each training run. We tried predicting it instead, with a simple formula fitted on other model sizes, so no watching would be needed.

What we found. For the middle three of five model sizes, the formula's timing was nearly as good as watching. For the smallest and largest, the formula had to guess beyond what it had seen, guessed wrong, and did no better than chance. Averaged across all five, it was no better than picking a random time.

Why it matters. The lesson: a forecast is only useful inside the range it was built from. Check where you are before trusting it.

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, 121 training runs (120 plus one anchor) plus K3's committed controls and oracle arm. The redesign, arms and kill tests were committed (9ad4795) before any run.

Program v2 Bucket N, item N22. Decisive computation: analysis/formula_timed_freeze.py. Output: analysis/formula_timed_freeze.json. Reproduce with python analysis/formula_timed_freeze.py (about ninety minutes on a throttled laptop CPU); --reuse re-derives every endpoint from the saved series.

The question

Every timed intervention in this programme was placed by an oracle, from each run's own observed transition, and K2 showed that is not enough: a single fixed step matched its saving. N22 asks whether a free formula -- predicting the transition from the model's settings, without watching the run -- can place an intervention as well as the oracle. The original design was amended before any run because on one setting a formula is a fixed step by construction; this is the redesign: K3's width ladder (16-192), where transitions differ five-fold, and D5's freeze of the recurrent matrices, whose cost is largest when the window ends at the transition (the critical period). A larger delay therefore means the window hit the critical period: the endpoint measures timing precision, not a benefit.

**A free formula times the sensitive moment only where its forecast is good.** Freezing part of a model for a short window hurts most just before it learns its task, so a bigger delay here means the window was well timed. Each line is one way of choosing when to freeze, across five model sizes. For the three middle sizes the free formula is almost as well timed as watching the run. For the smallest and largest it has to extrapolate, guesses wrong, and does no better than chance: averaged over all five, it is no better than random.

The formula: ln transition on ln width, fitted leave-one-width-out on K3's control runs. Three new arms, all with the same window length (a quarter of the predicted transition): formula-timed (window ends at the prediction), fixed-step (window ends at step 157, the ladder's median transition, for every width), and random. K3's oracle arm is reported beside them.

Kill tests, fixed before execution: pooled over width and seed, formula minus random includes zero or lies below it, or formula minus fixed-step includes zero. Anchor: K3's width-48 control reproduces. It holds.

Result: the kill test fires, on both counts

Pooled over `40` (width, seed) pairs	Paired delay difference
formula minus random	`-0.72` `[-5.26, +3.81]`
formula minus fixed-step	`-1.43` `[-5.30, +2.45]`

Pooled, the formula places the freeze no better than a random window or a single fixed step.

Why: it works where it can forecast and fails where it extrapolates

Width	Control transition	Formula's prediction	Oracle (K3)	Formula	Fixed step	Random
`16`	`272.8`	`367.7` (`+35%`)	`+28.6`	`+3.2`	`+21.4`	`+23.8`
`32`	`209.1`	`183.1` (`-12%`)	`+25.2`	`+19.8`	`+16.8`	`+10.8`
`48`	`155.2`	`140.2` (`-10%`)	`+19.0`	`+15.5`	`+16.6`	`+7.8`
`96`	`90.0`	`87.7` (`-3%`)	`+9.0`	`+8.8`	`+0.0`	`+4.1`
`192`	`50.5`	`62.3` (`+23%`)	`+2.5`	`+0.4`	`+0.0`	`+4.9`

(Mean delay to the transition, in steps; no intervals per width, eight seeds each.)

At the three interior widths, where the leave-one-out prediction is within 3%-12%, the formula-timed freeze lands near the oracle (+15.5 against +19.0 at width 48, +8.8 against +9.0 at 96) and above the random window at every one of them.
At the two end widths the formula must extrapolate, misses by 23%-35%, and its window falls after the transition, where the freeze costs almost nothing (+3.2, +0.4).
The fixed step does well only where it happens to sit near the transition (width 48, whose transition is 155 against the fixed 157), which is K2's lesson again.

Pooling the ends with the middle cancels the formula's advantage. This per-width reading is post-hoc and has no per-width intervals; it describes why the pooled test failed, not a finding of its own.

What stands

Kill test fires on both counts: pooled, formula-timed placement is indistinguishable from random and from a fixed step.
A free controller is only as good as its forecast. Within the fitted range the formula times the critical period nearly as well as the oracle; a leave-one-out fit fails exactly at the ends of the range, where it must extrapolate.
Practical reading: a formula can replace watching the run only inside the settings it was fitted on.

Limits

Five widths, eight seeds, one intervention whose value is its cost (the freeze is a probe of timing, not a useful manoeuvre).
The formula has one input (width); N14's fuller formula (width, lag, vocabulary) was not re-fitted at this rate.

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.
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.
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.
post hoc: Worked out after the fact, rather than decided in advance. We report such checks separately and never let them decide a result, because it is far too easy to find a pattern once you already know the answer.
probe: A small separate model trained to read information out of a bigger model's internals, used as a measuring instrument rather than as a product.
recurrent: A design that reads a sequence one item at a time, carrying memory forward. The main alternative is attention, which looks at everything at once.
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.
vocabulary: The set of distinct symbols a model can read and produce.
width: How many internal numbers a model uses at each layer. The usual way we vary model size in these experiments.