The trajectory is worth more where it is hardest to read

The scarce unit is not the idea. It is computational attention allocated under uncertainty.

I never wrote the sentence above, anywhere.

It is what I should have written. What I wrote instead was a question tossed at the end of a list of four, in the twentieth of the twenty eight sections of the last essay, past the point where the text had already said what it came to say: where to allocate the next 130 billion tokens? I asked the question, moved on, and never went back.

Four readers went back.

I asked for four independent critical readings of that third essay, each one done by a different artificial intelligence system, none of them knowing what the others had said. One of them wrote that the text almost loses its own strongest idea. I agree about the force, not about the absence. The idea has a section of its own there, and it even has a name. The defect is one of address: it lives in a place where nobody is paying attention any more.

But the correction does not fit inside that essay, and it took me a while to understand why. It is not a sentence that went missing.

It is the other side of the argument.

The third essay separates, halfway through, two things it had itself compressed at the start. One is being able to read where someone is heading. The other is getting there before that person. The first is a claim about information. The second is a claim about capacity. The first is necessary for the second, and neither one is enough on its own.

That essay spent almost all of itself on the legibility side.

This one is about the other side.

It is also considerably shorter, on purpose. Two of the four readings said the previous one was too long for the new ideas it carried, and that is a criticism you answer by writing less, not by explaining better.

The capacity to explore is not a quantity, it is a decision

In the third essay I wrote an expression for search time. It put the still relevant hypothesis space in the numerator, and the capacity to generate, test and validate candidates in the denominator.

I spent weeks looking at the denominator.

The numerator is the problem.

Because somebody chose which space goes in there. Ten thousand agents were not launched at every open problem in mathematics. They were pointed at a few.

By the company's own account, the campaign began after rumours that two Millennium Problems might have been solved, and the company credits the decision both to those rumours and to the performance of an internal model. We do not know what those rumours contained. We only know what the company says it did afterwards, and that is enough for the point.

What a rumour delivers, at best, is an indication of where to look. Not a proof, not a method, not a draft.

The third essay recorded this and treated it as scenery.

It is the subject.

A frontier infrastructure does not have infinite capacity. It has enormous capacity and a budget, and a budget forces choosing. Choosing where to spend capacity when you do not know which choice is the right one is the oldest problem there is in decision, and it has come back in a different unit of measure.

It is no longer researcher hours.

It is tokens, GPU-hours and energy.

Simon had already said this, and he was talking about something else

In 1971, in a lecture later published under the title Designing organizations for an information-rich world, Herbert Simon said that information consumes something, and that the something is the attention of whoever receives it. His conclusion is well known: a wealth of information creates a poverty of attention, and from that comes the need to allocate attention efficiently among the sources that compete for it.

The text sits in a volume edited by Martin Greenberger, published by the Johns Hopkins Press. It is worth saying where it comes from, because I spent the previous essay complaining about erased genealogies and it would be embarrassing to erase one here.

Simon was talking about human attention.

There is an awkward coincidence of vocabulary at this point, and I would rather disarm it now than leave it working for free in the text. The language models at the centre of this discussion have, inside them, a mechanism called attention. It is not the same thing. The attention mechanism of a transformer is a weighting operation between positions in a sequence, and it has nothing to do with scarcity, with opportunity cost or with giving something up.

The coincidence is too good to be taken seriously.

I am not going to use it as an argument.

What changed since 1971 is not the mechanism. It is that scarce attention, in Simon's sense, stopped being only human. There is today a finite quantity of frontier computing capacity in the world, it is expensive, it is contested, and somebody decides every day where to point it. This is not a metaphor, and not an analogy with the brain.

It is a budget line.

This essay has a single equation, and it is not mine

The previous essay had twelve.

I wrote there myself that a well formatted equation has the unpleasant habit of looking more established than the prose around it. I wrote that and then wrote twelve equations. One of the readings noticed. It was right.

So this is the only one, and the idea inside it is from 1966.

In Information Value Theory, published in the IEEE Transactions on Systems Science and Cybernetics, Ronald Howard proposed something that Shannon's information theory did not do. Shannon measures quantity of information, and the measure depends only on the probabilistic structure. Howard observed that no theory built only on the probabilities of outcomes, without considering the consequences of those outcomes, could possibly be adequate for deciding anything. The value of a signal, for him, depends on what it changes in the decision of whoever receives it.

We can write it like this:

V(s) represents the value of the signal s. a* represents the best allocation of resources I could choose without it, and a*(s), the best allocation after receiving it. U represents the expected outcome of an allocation. The value of the signal is the difference between the two, and not a property of the signal.

Notice what that equation does not say.

It does not claim that true information is worth more than false information. It does not claim that rare information is worth more than common information. It does not even claim that information about the future is worth more than information about the past.

It says one thing only, and it is uncomfortable:

information that changes no decision is worth zero.

Even when true.

Even when rare.

Even when expensive to obtain.

This is where I see what was missing in the previous essay. There I wrote the information of the trajectory as a reduction of uncertainty, in Shannon's classical form: the uncertainty about where to look, minus the uncertainty that remains after considering the ballast. That measures how much uncertainty the trajectory removed.

I never asked whether the removal changed any allocation.

It was Howard who asked that question, and he asked it sixty years ago.

Generating got cheap, and there is a measure of it

The economic part of this discussion tends to be conducted with adjectives. It is worth looking at a number.

In 2024, Bradley Brown, Jordan Juravsky, Ryan Ehrlich, Ronald Clark, Quoc Le, Christopher Ré and Azalia Mirhoseini, of Stanford, Oxford and Google DeepMind, published a paper with the distinctly unceremonious title Large Language Monkeys. The question was simple: instead of training a bigger model, what happens if you let the same model try many times?

They measured coverage, that is, the fraction of problems for which at least one of the attempts is correct, and watched that number grow across four orders of magnitude of attempts. On SWE-bench Lite, a set of real software engineering tasks, DeepSeek-Coder-V2-Instruct solved 15.9 per cent of the problems with one sample and 56 per cent with 250 samples.

That is the result usually quoted, and it says less than it appears to. Software engineering tasks come with tests, and a test decides on its own. In that set, therefore, coverage counts almost as result: whoever generated 250 attempts can run them all and keep the one that passes.

The other finding is the one that matters, and it comes from the same work.

The authors record that the common methods for picking an answer out of a collection of attempts, majority voting and reward models, plateau after several hundred samples in the domains that have no automatic verifier. There, coverage keeps climbing and the ability to make use of it stops climbing alongside it.

And there is a detail of method that changes the meaning of the first number, and that I would not have noticed had I not been looking for it.

Coverage is measured with the answer key in hand.

You only know that one of the 250 attempts was right because you, the evaluator, know what the answer was. Where there is no automatic test and no answer key, 250 attempts with one correct answer inside and no way of identifying it are worth exactly the same as zero attempts.

It is one study, on one set of tasks, with models from that year. It is not a law, and I do not treat it as one.

But the shape of the finding is what interests me, and it comes before any specific number: generating scales, choosing does not scale with it.

The bottleneck did not disappear.

It moved.

Lean is a verifier, and perhaps that is why that worked

Back to the case that took up the previous essay.

In the company's own account, the result on Navier–Stokes appeared roughly 88 hours after the first agents were launched, and the formalisation and verification in Lean consumed another 17. I treated that second number as an operational detail.

It is not a detail.

Lean is a proof assistant. It accepts or it does not accept, and its decision does not depend on taste, on reputation, on who signs the paper or on how elegant the argument looks. A swarm of agents working inside formalisable mathematics has, at the end of the line, an oracle.

The account says no more than that, and stretching it would be cheating. It records that the result appeared first and that the formalisation came afterwards, which describes an oracle consulted at the end, and not necessarily inside the search. The difference matters for what comes next.

Ten thousand concurrent agents, in the number the company reports.

In a domain with a mechanical verifier, they are one thing.

In a domain without one, they are another.

What I propose here is a conjecture, and it is mine.

Where a mechanical acceptance test exists, scaling generation converts into result almost directly, because selecting costs in proportion to the number of candidates and not to the number of hypotheses about where to look, and it is paid for out of the same budget that buys the generation.

Where that test does not exist, scaling generation produces more candidates and no additional capacity to choose among them, because there is nothing to spend budget on in order to produce the choice.

Selecting is not free even in the first case, and the number above says what it cost: seventeen hours against eighty eight.

The difference between the two cases is not the price of selection.

It is the existence of a price.

And in the second case the cost migrates, in good part, to the decision about where to look before generating.

And this is where a prediction I made in the previous text changes meaning, without any new fact having entered. What entered was the definition from 1966, and it reorders what I had already written.

I wrote there that the hypothesis might work extraordinarily well in programming, reasonably well in scientific investigation and very badly in literary creation. I still think that is true about the ease of predicting.

It has stopped seeming true to me about the value of predicting.

Where a verifier exists, the human trajectory is a convenience. It brings forward the work of a system that, in the limit, could try everything and let the oracle decide. Where no verifier exists, the trajectory of someone who knows the terrain may be the only available criterion of priority.

The trajectory is worth more exactly where it is hardest to read.

The two sentences do not contradict each other, and the distinction between them is the same one between Shannon and Howard. The first is about quantity of information. The second is about its price. Within one and the same decision problem the two move together, and more information is never worth less. Between different decision problems, no: the same gain in precision is worth the entire window where there was no way to choose, and worth almost nothing where the oracle would choose on its own.

The inversion lives in that passage, and not inside any isolated domain.

This produces a prediction that can fail, and it is worth saying how large the risk is, because a prediction that only loses in an extreme case risks nothing.

Rank the domains by the precision with which a person's trajectory can be read. Rank the same domains by the gain to whoever reads it. The thesis claims the two rankings run in opposite directions. With the three domains I listed in the previous text there are six possible orderings, and in three of them the two run in the same direction.

The thesis loses in half of the possible outcomes, and not only in the case where the two rankings turn out identical.

The strongest objection to this essay is that it is sixty years old

I am going to list three ways of my being mistaken, because the list is more honest than the defence. And then a fourth thing, which is not one of them.

The first, and the most serious, is that none of this is new. Choosing where to spend limited resources under uncertainty has a dense and old literature. Bandit problems, Bayesian experimental design, optimisation under uncertainty, expected value of sample information. An acquisition function, in Bayesian optimisation, is literally a rule for deciding where to spend the next measurement. This has existed since before me, and it is taught.

I concede it entirely.

What changed is not the problem. It is who holds the budget, and how much that budget suddenly grew.

And the exchange is not only one of size.

In that literature, whoever pays for the next measurement is whoever holds the hypothesis. Here, whoever pays is a third party, who also receives the signal about where to measure.

The second is that verifiers may get cheap everywhere. There is serious work on process reward models and on learned verifiers, and if they work well in open domains, the asymmetry I described above dissolves, and the central argument of this text goes with it. I record that as a failure condition, not as a caveat.

The third is that the allocation may not need me. Perhaps the public state of a field, on its own, already indicates where to look with sufficient precision, and the individual trajectory adds little on top of that. That is exactly the comparison the experimental design has to make, and it is the reason it needs four compared systems and not two: one with what the person published, one with the public state of the field, one with both, one with both plus the trace.

The whole design goes in the preprint, which is where it can be preregistered before I have any result at all.

The fourth thing is not a way of my being wrong. It is what happens if I am right, and I have no good answer to it.

If the scarce resource is the decision about where to spend capacity, and if that decision can be read in the trajectory of whoever is working, then the part of my work that has economic value begins to migrate from what I finish to where I am looking. Incomplete research has always been worth little. Perhaps it comes to be worth more incomplete than finished, to whoever is not me.

I do not know what that does to a person who does this for a living.

I record that the question exists.

What this does to the question from the second essay

In the second text of this series I wrote about an uncomfortable possibility: a structure can offer prosperity and go on concentrating sovereignty. The idea is that income keeps coming in, wealth stops forming and control closes, without any of it requiring villainy.

That argument was about property and mobility.

It gets stranger when the object is computational attention.

To govern data is to govern the past. It is to decide who keeps what already happened, for how long, and under what conditions. To govern allocation is another thing: it is to decide what will still be attempted. The first is a question of archive. The second is a question of future, and we have no legal vocabulary for it at all.

Nobody needs improper access to my files for this to happen. It is enough that I produce, in the normal course of work, sufficient signals about where it is worth looking, and that somebody else has the budget to act on those signals in the week they appear.

That was the thesis of the first essay, and it had a name I borrowed from an internet community of twenty years ago. Obsolete vanguardism. The idea that one can go on being the vanguard and still stop harvesting anything for it.

At that moment I thought I was talking about copying.

Then I thought I was talking about inference.

Perhaps I am talking about budget.

What goes somewhere else

Two things matured in the discussions of these days and do not fit here, and I say where they go so as not to abandon them in silence.

The first is the experimental design. The hypothesis of the third essay needs four compared systems, not two, and it needs a condition that almost slipped past me: the model used in the test cannot have been trained on data later than the date one is trying to predict.

A system that has already seen the future we ask it to estimate is not predicting, it is remembering.

That, plus defining the regions before the test and matching the arms by volume and recency, is protocol, and a preregistered protocol is not a genre of essay. It is a preprint, and it will be the fourth artefact of this series, not the fifth text of it.

The second is a question of form, and it interests me more than I expected. In the first essay I provisionally called generating function what I now call trajectory inference, and I abandoned the name because it committed me to a stable regularity existing inside me. It turns out there is an honest formal object there, and it is not a generator. It is an evaluator: a function that, given my history, assigns a probability that I would accept any given candidate.

The difference has consequences, and they favour whoever writes.

A function that only scores candidates cannot produce any. It merely orders what a generic generator has already produced. If the ballast feeds the evaluator and never the generator, then the copying reading dies by typing, and not by rhetoric. I spent two sections of the previous essay trying to say this in prose.

The form of it also goes to the preprint.

Back to the question that stayed

Where to allocate the next 130 billion tokens is a good question.

As someone who studied computer engineering, I know it is the only one of the four I had listed in that section that was not rhetorical. The other three described a problem. This one asks for a number, a date and a signature.

As a neuroscientist, I recognise the shape of the problem, and I stop at the border of the analogy: allocating a limited resource under uncertainty is what a nervous system does all day long, and the resemblance ends exactly there, because an inference budget is not an organism and treating the two as relatives would be the kind of shortcut I have spent three essays avoiding.

As a psychologist, I distrust any criterion of priority that presents itself as neutral. Every allocation rule carries a theory about what deserves to exist, and rules like that tend to be written by people already well served.

And as a clinical psychologist, there is one last thing.

We also allocate attention under uncertainty, and it is literally what we do: in an hour of session, choosing which hypothesis about a person is worth pursuing and which can wait until next week. I choose without an answer key, like everyone who chooses under uncertainty, and a good share of those bets do not come off. The difference is that, when the region I chose was not the most promising one, the cost is not measured in tokens.

Perhaps that is why this question bothers me the way it does.

It can only be asked by whoever has the 130 billion.

And the prior question, which is simpler and a good deal more uncomfortable, remains without an owner:

who decides what deserves to be attempted?