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

Growth Saves Nothing Here

By Joshua Bolick, Awareness Software Group ~10 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: 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. Growing a model during training saved a quarter of the compute on one task, then failed on a second, slower one, and we suspected the growth timings were set for the fast task. So we rescaled them and tried again.

What we found. It still saved nothing that mattered. Growing looked cheap next to training the full-size model, but on this task a medium-sized model trained at one fixed size did just as well for the same compute, and reached the target more often. Our comparison rule had quietly counted only the full-size model as the alternative.

Why it matters. The lesson: the right baseline is the cheapest option that actually works on the task in hand. On the first task only the big model worked, which is why growing paid off there.

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, 67 training runs of 6000 steps. The design and kill test were committed (c3e94bd) before any run; two false alarms in the growth check were fixed in separate commits (0cb5b0a, 343f8a5) before the run reported here, with no change to what is trained or measured.

Program v2 Bucket O, item O28. Decisive computation: analysis/progressive_width_scaled.py (O5's code, grid scaled). Output: analysis/progressive_width_scaled.json. Post-hoc, changing no verdict: analysis/progressive_width_scaled_posthoc.py -> analysis/progressive_width_scaled_posthoc.json.

The question

O5 found growing a GRU 24 -> 48 -> 96 saved 26% of the FLOPs to held-out accuracy 0.95 on a copy task. O27 reran it on modular sum and no schedule reached the target, because O5's growth grid was built for a task learned seven times faster. O28 scales the grid by that factor (s1 in {350, 700, 1400}, s2 - s1 in {350, 700, 1400}), runs 6000 steps, and saves every curve. Arms, endpoint and kill test are O5's: progressive minus the best fixed width, or minus random growth, has an interval including zero or above it.

**On the second task, a fixed medium model is as cheap as growing, and more reliable.** The growing recipe, with its timing rescaled for this slower task, against models trained at one fixed size. Bars show the compute to reach 95% accuracy averaged over the runs that reached it; the fraction in each label is how many of eight did. The medium fixed model reaches the target in seven of eight runs for about the same compute as growing does in five. Growing only looks cheaper next to the full-size model, which this task did not need.

The growth check (logits unchanged by growth) raised false alarms twice from float32 rounding once logits grew large; it now compares the largest difference with the logits' scale. Both fixes are committed separately.

Result: the kill test fires

Arm	Reached `0.95`	FLOPs to `0.95` (mean, where reached)	Final accuracy
fixed-24	`5/8`	`19.6` G	`0.732`
fixed-48	`7/8`	`50.2` G	`0.937`
fixed-96	`8/8`	`222.6` G	`1.000`
progressive (grow at `1400`, `2800`)	`5/8`	`57.3` G	`0.750`
random growth	`4/8`	`76.4` G	`0.669`

Paired difference	FLOPs
progressive minus random growth	`-47.0` G `[-109.4, +15.4]` -- includes zero
progressive minus fixed-96 (O5's "best fixed width")	`-177.4` G `[-310.4, -44.3]`

The kill test fires on the random-growth comparison: the scaled schedule does not beat a random one.

The comparison O5's rule left out (post-hoc)

O5's code names as the "best fixed width" only an arm that reaches the target on all eight receivers, which here leaves fixed-96, the most expensive. On this task the narrow widths mostly reach the target and are far cheaper. On the receivers where both reached it:

Progressive minus	Pairs	FLOPs
fixed-24	`5`	`+37.7` G `[-35.3, +110.7]`
fixed-48	`5`	`+4.7` G `[-64.0, +73.4]`

Against the narrow widths, growth saves nothing, and it is less reliable (5/8 reach the target against fixed-48's 7/8; mean final accuracy 0.75 against 0.94). O5's rule was not wrong on O5's own task, where the narrow widths almost never reached the target; it was a rule that could pick the most expensive arm as "cheapest" the moment a narrow model sufficed.

What stands

Kill test fires: on the second task the scaled growth schedule does not beat a random one.
Growth saves nothing against the cheapest fixed width that mostly works (fixed-48), and is less reliable.
O5's 26% remains a one-task result, from a task where the model needed its full width. O5 carries a second banner. The candidate outside-venue piece on it is withdrawn.
Method: a "best fixed alternative" rule that demands every seed reach the target can select the most expensive arm; compare against each fixed arm and report its reliability.

Limits

Eight receivers, of which five reached the target under growth; paired intervals rest on those.

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.
GRU: Gated Recurrent Unit. A compact design for processing sequences one item at a time, with internal switches controlling what it keeps in memory.
held-out: Data the model was never trained on, kept back specifically to test it. Scoring a model on data it has already seen measures memorisation, not learning.
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.
logits: The raw scores a model produces for each possible answer before they are turned into probabilities.
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.
reliability: How often something works on an individual case, as opposed to how well it does on average. The two can differ a lot, and only one of them tells you what to expect next time.
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.