Abundance

Essay IV

Abundance

On what becomes of a research organisation when thinking costs nothing

I. A Warning, Then a Thought Experiment

This text is speculative, and I prefer to announce it rather than let it be discovered.

The three essays that precede it bore on situations observable today. This one bears on things that do not yet exist, and the history of technological projections is a graveyard — the paperless office, the end of business travel, the disappearance of large retail and the coming of the self-driving car were all announced for dates that have all passed. There is a structural reason for these failures: we know fairly well what a technology permits, and very poorly what organisations do with it.

I do not claim, then, to describe what will happen. I claim to describe what becomes possible, what is different, and what has the advantage of being arguable.

Here is the thought experiment.

Suppose a research organisation could produce, at negligible cost and with no delay, any analysis of the existing: a literature synthesis, a patent review, a state of the art, a comparison of methods, the reconstruction of an internal history. Suppose it could frame as many hypotheses as it likes, as well argued as it likes. Suppose it could simulate everything simulable, and paid in real time only for what demands matter.

The assumption is nothing extravagant: several fields already live roughly in that situation, and the others are approaching it with a lag of a few years.

Now the question: what, in the present organisation of research, no longer has reason to exist?

I shall argue that the answer is: almost everything. These structures are not bad; they are all, without exception, optimised answers to a constraint of scarcity that has just disappeared.

And I shall argue a second thing, less obvious: that abundance does not make selection less important. It makes it infinitely more important, and it requires moving it far upstream, onto an object no organisation treats today as an object of work.

II. Everything Scarcity Built

An organisation is an answer to constraints. When the constraints change and the organisation does not, it goes on solving a problem that no longer arises.

Let us look, then, at what our research structures were solving.

Selection upstream, massive and final.

When every lead explored is expensive, one must sort before exploring. Hence the considerable weight of the framing phase, the selection committees, the justification files, the feasibility reviews. Enormous investment goes into avoiding commitment to a bad direction, because the wrong direction costs years.

This arrangement has a consequence never discussed: it eliminates the leads whose interest cannot be demonstrated before having explored them. That is, mechanically, the most original ones. An organisation that demands justification upstream selects for plausibility, never for surprise.

That was the price to pay. It is no longer one if exploring costs a day.

The programme as unit of work.

All organised research works by programmes: a multi-year object, endowed with a budget, a team, a head, objectives. It is the unit of management, the unit of reporting, the unit of decision.

Why the programme and not the question? Because a fixed cost had to be amortised. Setting up a team, acquiring equipment, developing a specific competence — none of that was justified except over several years. The unit of work was set on the amortisation period of the fixed cost, not on the nature of what was being sought.

The fixed cost of intellectual exploration has just fallen to zero. The fixed cost of experimentation has not — but it now concerns only the fraction of what one explores that one decides to test.

Long cycles and widely spaced reviews.

A programme is reviewed every six or twelve months. Why that frequency? Because nothing informative happened between two reviews. The time needed to obtain interpretable results was of that order, and convening a committee to note that one is still waiting made no sense.

That reasoning still holds for the experimental part. It no longer holds at all for the upstream part, where a team’s state of knowledge can change substantially in three weeks.

The prudence of the bets.

A classical research portfolio comprises few projects, each endowed with substantial means, selected for their probability of success. It is a risk-averse structure, and it is perfectly rational when every bet is expensive: with ten possible bets and the budget for three, one must choose the three surest.

That rationality reverses completely when the cost of an exploratory bet collapses. With the budget for three hundred probes and ten experiments, the optimal strategy is no longer to choose the surest — it is to multiply asymmetric bets, those whose cost is low and whose potential gain is high, accepting that most will give nothing.

No research organisation is structured for that. Neither its processes, nor its committees, nor its culture, nor its indicators.

Hierarchy by seniority.

It is a direct consequence of the structure of apprenticeship described elsewhere. If judgment is acquired over fifteen years of production, then seniority is a reasonable indicator of the quality of judgment, and organising authority by seniority is an informed choice.

That correlation is breaking, and with it the rational ground of a good part of the hierarchical organisation of research.

And finally, narrow specialisation.

When reading a field’s literature takes years, one can cover only one. Specialisation is first of all a constraint of reading time. The whole disciplinary structure of research (departments, journals, congresses, careers) is built on the cost of entering a body of literature.

That cost has just fallen considerably. Not disappeared: understanding a field deeply remains long. But reaching a level of competence sufficient to spot a useful analogy, put a pertinent question, identify what has already been done elsewhere — that level has become accessible in a few days instead of a few years.

It is perhaps the change with the heaviest consequences, and I shall come back to it.

There is the inventory. Six structures, all coherent with one another, all optimised for a world in which producing thought was expensive. That world lasted three centuries. It has just ended, and nothing has moved.

III. Abundance Does Not Remove Scarcity, It Displaces It

One should be wary of the word abundance, which suggests that everything becomes easy. That is not what happens.

In every system, something is scarce. When a resource ceases to be, scarcity does not disappear: it moves to the next element in the chain, and that element becomes the point of tension.

Economic history is made of these displacements. When mechanical energy became abundant, scarcity passed to the organisation of work. When information became abundant, it passed to attention. Each time, organisations took a generation to notice, because they went on optimising the resource that had become abundant — that was what they knew how to do.

Where does scarcity go here? It goes, successively, to three places.

First to judgment: the capacity to say what is good. That is the subject of the first essay and I shall not return to it.

Then to physical time: the capacity to validate in the real. That is the subject of the third.

And finally, the object of this text, to the question.

Here is what I want to argue. When framing a hypothesis costs a day and testing one costs six months, value no longer lies in the hypotheses. It lies a notch higher, in the choice of what one looks for.

That looks abstract. It is not at all, and the best way to see it is to consider what an organisation does today with its questions.

The answer is: nothing. Almost no research organisation treats its questions as an object of management. It manages projects, programmes, budgets, competences, equipment, partnerships. It does not manage the list of what it seeks to know.

Ask a research director for the list of their organisation’s open questions, those they would like an answer to and that figure in no current project. They will give you an improvised, personal answer, different from the one their predecessor or their neighbour would have given. That document does not exist.

It does not exist because it was of no use. When only three leads can be explored, the list of questions merges with the list of programmes: no point keeping both. The question was incorporated into the project at its birth, and then disappeared as a distinct object.

What changes is that the ratio between the two has just gone from one to one to one to a hundred. A hundred questions can now be explored in order to work up one. The list of questions stops being redundant with the list of projects: it becomes an autonomous object, and by far the more precious of the two.

An organisation that knew what it seeks to know would have a considerable advantage over an organisation that knows only what it is doing.

That is, I believe, the most useful restatement in this whole text.

IV. The Question as Unit of Work

What makes a good question, no one can say, and that is telling: we have fairly elaborate criteria for evaluating an answer — validity, reproducibility, significance — and practically none for evaluating a question. It fell to individual talent, to intuition, to flair. Certain researchers were said to have a gift for putting the right questions, and that was an elegant way of admitting we did not know what we were talking about.

It seems to me nonetheless that one can advance, and I propose four properties. They are not a method; they are candidates for discussion.

A good question is one whose two possible answers change something.

It is the most discriminating and the most violent criterion. Take any research question under way in your organisation and ask: if the answer is yes, what do we do? if it is no, what do we do? If both branches lead to the same action, the question is worth nothing, whatever its scientific interest.

This criterion eliminates a considerable proportion of what occupies industrial laboratories. Good work, often, but confirmatory: it produces knowledge that modifies no decision.

A good question is one whose answer no one knows and many believe they know.

That is where asymmetric value lies. An open question recognised as such is already being worked on by everyone; the return on marginal effort there is low. A question the consensus holds to be closed when it is not offers a return beyond comparison, because no one is working on it.

Such questions exist in great number in every field. They are hard to spot because seeing them requires being able to doubt what everyone takes for granted — which is precisely what a disciplinary training discourages.

A good question is one where one could say what would settle it.

It is the criterion of testability, and it is the most operational of the four. A question to which no discriminating experiment can be attached is a topic of discussion. The distinction is old and it remains the best filter available.

A good question is one whose answer has a lifespan.

This one is less classical and I believe it important. Some answers are good for three years, others for thirty. In an industrial context, a question whose answer will be obsolete before having been exploited is a badly chosen question, whatever its intrinsic quality. No one ever evaluates that dimension.

What I describe here is not a methodological innovation. It is what the best researchers do, informally and without formulating it — those said to have the flair. The proposition is simply that what fell to individual talent should become an object of collective work, for the reason running through these four texts: what was scarce and therefore precious in a few becomes the critical resource of the whole.

And there is a still more pressing reason to attend to it. A generative system is extraordinarily good at answering and remarkably mediocre at asking. It will produce a thousand answers to your question; it will never tell you that it is not the right question. That asymmetry is structural, it follows from the way these systems are built, and it will not be corrected by incremental improvement.

The only intellectual work one can be reasonably certain will stay human for a long time is therefore the work of the question. It is also the one no one is trained in, that no one evaluates, and that appears in no job description.

V. What History Says About Abundances

Before going further, it is worth looking at what happened the previous times. This is not the first abundance, and the previous ones have regularities.

Printing. In half a century, the cost of reproducing a text collapses. Access to knowledge will come later. The immediate consequence is a proliferation of texts of very unequal quality, in which contemporaries complain abundantly of no longer knowing what to read. Sixteenth-century scholars left pages on that feeling of being submerged, in terms that resemble today’s in a troubling way.

What solved the problem was not a technology. It was institutions of sorting: the catalogue, the organised library, the publishing house with its line, criticism, later the peer-reviewed journal. All have the same function — deciding what deserves attention — and all took between fifty and two hundred years to constitute themselves.

The lesson is double, and both halves matter. The first: when production becomes abundant, value migrates to selection, and new institutions are created to provide it. The second, less encouraging: those institutions take a very long time to appear, and the interval is a period of real confusion during which a great many bad things circulate unimpeded.

Numerical computation. In the nineteen-seventies and eighties, computing capacity becomes affordable and then commonplace. Whole disciplines, from fluid mechanics to quantitative finance by way of meteorology and theoretical chemistry, see the cost of what was their central operation collapse.

What happened next is instructive. At first, everyone did more of what they were already doing: more simulations, more scenarios, finer models. The gains were real and modest. The leap came only when people stopped simulating what they already knew how to describe and began exploring spaces they could not traverse otherwise — that is, when the question put changed, not only the power available.

That interval between access to the capacity and the reformulation of the questions was, depending on the field, ten to twenty years. It was the time needed for a generation trained under the old regime to give way.

Genomic sequencing. The case closest to what concerns us, because it is recent and documented. In fifteen years, the cost of sequencing a human genome goes from several hundred million dollars to a few hundred. The fall is faster than that of electronic components over the same period.

The bottleneck moved immediately — and not where it was expected. It did not pass to storage, nor to computation, which kept up roughly. It passed to interpretation. People found themselves with quantities of data whose production cost nothing any more and from which no one knew how to draw an actionable conclusion. A good part of the promises of personalised medicine broke on that gap, which was not a technological gap but a gap in the capacity to make sense.

The regularity, in these three cases, is the same and it is clean. When a capacity to produce becomes abundant, what becomes scarce and dear is the capacity to decide what to do with it. And that capacity cannot be bought: it is built slowly, through institutions, methods and people trained expressly.

There is a second regularity, more disturbing. In each of these episodes, the established players were less well placed than the new entrants. Their competence consisted largely in mastery of the operation that had become free. Printers did not dominate publishing. The best analytical calculators did not dominate simulation. Sequencing laboratories do not dominate clinical genomics.

It is a serious reason not to regard an acquired advantage as protection.

VI. What Becomes of the Portfolio

A classical research portfolio looks like this: eight to fifteen programmes, each endowed with several hundred thousand to several million euros, committed over three to five years, selected in a heavy framing phase, revised annually, and stopped rarely — because stopping is costly in political capital and because the cost already committed weighs on the decision when it should not.

That structure is the structure of an investor who cannot afford diversification. It is optimal when every bet is expensive, information on its quality arrives late, and the number of possible bets is limited.

None of those three conditions is still true on the upstream side.

What becomes possible is a two-tier structure with no equivalent in the present organisation.

The tier of probes. A large number of very cheap explorations — a few person-days each — bearing on questions one does not know to be worth anything. Each probe consists in working the question up to the level of what is already known: what is known, who has tried, what failed and why, what experiment would settle it, what it would cost. The deliverable is an estimate of the value of going further.

At the scale of a mid-sized organisation, one is speaking of several hundred probes a year for a cost below that of a single classical programme.

The tier of commitments. The small number of heavy programmes, endowed as they are today, but selected on an entirely different basis: no longer from proposals written by those who want to run them, but from the probes that revealed something.

What that structure does is well known to investors and is not to research directorates: it buys information before buying commitment. The probe serves to reduce the uncertainty about the programme’s value, not to find the answer — and it is an investment whose return is higher the greater the initial uncertainty.

Two counter-intuitive consequences follow, and they run head-on into the culture of research organisations.

First consequence: the failure rate of probes must be very high.

If eighty per cent of your probes conclude that it is worth continuing, you are not probing — you are justifying programmes you had already decided on. The healthy failure rate, in this kind of arrangement, lies between ninety and ninety-five per cent.

That is culturally very difficult. There is no research organisation where one can announce that an activity must fail nine times out of ten to work properly. The very vocabulary is missing: we have no word for an exploration correctly conducted and concluding that there is no interest. We say it came to nothing, which is false — it gave exactly what it was asked to give.

The word exists nonetheless, elsewhere. In particle physics, a search that finds nothing produces an exclusion limit: it establishes that if the object sought exists, its properties lie outside the domain explored. It is a result. It is published, it is cited, it narrows the space in which others will have to look, and the career of whoever signs it does not suffer. A research organisation able to produce and keep its exclusion limits would have settled half the problem described in these pages.

Second consequence: the value of the arrangement is not measured on the probes that come to something, but on the programmes one did not launch.

It is the asymmetry already met twice: avoided errors are not observable. An organisation that, thanks to three hundred probes, avoided launching two programmes that would have failed after three years has saved several million euros — and has strictly nothing to show.

There is no elegant solution to that problem. There is an ugly solution that works: decide in advance, and write down, which programmes one would have launched in the absence of probes. Constitute the counterfactual before knowing the result. It is tedious and it is the only way of making visible a value that will otherwise stay invisible for ever.

Experimental physics has practised this for decades under the name of blind analysis. The selection criteria and the treatment method are frozen before looking at the data, because it was found that researchers adjusted their cuts until the expected result appeared, without bad faith and without noticing. The arrangement supposes no dishonesty. It supposes distrusting oneself, which is another matter and a harder one.

This reasoning has a limit, and it counts.

All of it supposes that a probe is informative — that is, that a documentary exploration really reduces the uncertainty about a programme’s value. That is true in fields where the literature is rich and where the failure of others is published. It is much less true in fields where most of what matters is not published: because it is confidential, because failures are never reported, or because the determining knowledge is knowledge of the hand.

In those fields, the documentary probe says almost nothing, and one must move very quickly to an experimental probe — dearer, less parallelisable, which considerably reduces the reach of the reasoning.

The question to ask is therefore: in my field, what fraction of what will determine a programme’s success is accessible without putting one’s hands in the matter? If the answer is half, this arrangement changes everything. If it is five per cent, it will not change much.

VII. What Becomes of the Organisation

I shall describe, with the necessary precautions, what a research organisation designed for abundance might look like. It is an exercise: a way of making concrete the consequences of what precedes.

It would be smaller and much denser.

The number of people needed to produce material falls sharply. The number needed to arbitrate, test and validate falls little or not at all. The pyramid deforms: less wide at the base, roughly stable at the top, and above all much shorter. The intermediate levels — those whose main function was to circulate, aggregate and format information between bottom and top — lose most of their reason to be.

It is the most predictable and the most painful consequence, and it would be dishonest to present it otherwise.

It would keep a bank of questions.

An object that exists nowhere today: the living, prioritised list of what the organisation seeks to know, distinct from the list of what it does. Fed by everyone, arbitrated by few, revised often. Each question carrying its status — open, probed, committed, closed — and above all, for closed questions, the trace of what closed them.

That object would have a property nothing has today: it would survive the people. Knowledge about what is worth looking for is currently held by a few individuals and disappears with them. There is no reason for it to be so, except that no one ever considered that it ought to be written down.

It would document its rejections.

It is the point I come back to in all four texts, because it is the one on which everything else depends. An organisation that keeps only its positive decisions cannot learn: it holds only half the data, and the less informative half of the two.

Concretely: for each question set aside, three lines — why, on what assumption, what would reopen it. The third line is the one with value. It turns a final rejection into a conditional rejection, and it makes it possible, two years later, to reopen automatically what should be reopened when the condition changes.

It would organise its cycles on two distinct rhythms.

A fast rhythm on the upstream, a few weeks, because the state of knowledge changes fast there. A slow rhythm on the downstream, set on physical time, because there is no point convening a committee to note that a cohort is under way.

Today, those two rhythms are merged in a single cycle, generally annual, which is too slow for one and too fast for the other.

It would have an identified sorting function.

With a holder, written criteria, a budget and an evaluation. It is perhaps the most difficult change, because it explicitly creates a power that existed only implicitly — and because it exposes that power to challenge, which is at once its interest and the reason no one wants to create it.

And it would be much less disciplinary.

That is the consequence of the collapse in the cost of entering a body of literature. If understanding a neighbouring field well enough no longer takes years, then the logic that produced departments, specialities and linear careers loses its ground.

What becomes profitable instead is the profile that knows how to put questions at the intersection — someone whose competence is not depth in one field but the capacity to see that a problem solved here resembles a problem open over there. That profile has always existed, it has always been rare, and it has always been badly treated by institutions that did not know where to file it.

It is becoming the most useful profile in a research organisation, and practically no career structure knows how to recognise it.

VIII. Who Decides What Is Looked For

If value migrates towards the question, then a question of governance becomes inevitable, and it has never been put: who has the right to decide what the organisation seeks to know?

Today, the answer is diffuse to the point of not existing. Questions are born at the bottom — a researcher takes an interest in something — and come up in the form of project proposals. They are filtered by committees that evaluate not the question but the project embodying it: its feasibility, its budget, its alignment with the declared strategy, the credibility of whoever carries it.

That arrangement has a property that must be seen clearly: it never selects among questions, it selects among those that found someone to carry them. An excellent question no one wants to carry does not exist. A mediocre question defended by someone convincing comes up.

That was acceptable when carrying a question cost years — the willingness to commit was itself a signal of quality, and probably a good one. It is no longer acceptable when exploring costs a day, because the signal disappears without the filter disappearing.

Three models of governance are possible, and one must choose.

The top-down model. Management sets the questions, the teams work them up. It has the advantage of strategic coherence and it has a known defect: leaders put the questions of their time, those whose pertinence is already established, and never those that would come from an anomaly observed in a laboratory. It produces research that is perfectly aligned and structurally incapable of surprising.

The bottom-up model, which is the present model, inherited from the academic world. It picks up weak signals and it has the symmetrical defect: it produces no coherence, it follows individual interests and disciplinary fashions, and it makes arbitration impossible since there is no common criterion for comparing two questions coming from two different universes.

A third model, which to my knowledge no one has built: the question as a common good, fed by all and arbitrated explicitly by an identified function, with written criteria and an accounting for the quality of past arbitrations.

It is what I called above the bank of questions, and I insist on the point that makes it different from a simple list: it separates the origin of a question from the working of it. Anyone can deposit a question; it is not necessarily they who will work it up. That separation, which looks innocuous, breaks the link between the value of a question and its author’s capacity to defend it — which is exactly the bias of the present system.

It has a second virtue, less obvious. It makes it possible for an organisation to recognise the value of someone who puts good questions without ever carrying them out. That profile exists in every house; it is invisible today, sometimes regarded as a dilettante, and it is becoming one of the most precious.

There remains the main difficulty, and I do not underestimate it: creating an explicit sorting function amounts to creating a power. That power will be challenged, and it must be — a sorting that cannot be challenged is a sorting that does not improve. But one must then accept that the challenge be organised rather than muffled, which supposes that the criteria be written and that past decisions be revisitable.

That is very exactly what learned organisations have refused to do for a century, and for the reasons described in the first of these texts. One always falls back to the same place.

IX. What Becomes of the Scientist

An organisation is nothing other than people.

The scientific trade as it constituted itself in the twentieth century rests on a tacit agreement between three elements: a competence that is rare and long to acquire, considerable autonomy in the conduct of the work, and a recognition founded on visible production.

All three are moving.

The competence stays long to acquire in its tacit part, and becomes quick to acquire in its explicit part. The division between the two is shifting, and it is shifting against what is transmitted by teaching.

Autonomy is paradoxically threatened by abundance. An autonomous researcher, under the old regime, was autonomous because no one could follow what they did without devoting as much time to it as they did. That protective opacity is crumbling: it becomes possible, for a third party, to form in a few days an informed opinion on a field that previously took years. Competence no longer protects autonomy as it did.

Recognition finds itself deprived of its main support, since visible production ceases to discriminate.

What I describe here is a destabilisation, and I do not want to present it as good news in disguise. It will be lived through harshly by many people, and part of what will be lost deserved to be kept.

But one must also see what opens, because it would be dishonest not to speak of it.

The scientific trade, as it is actually practised in an industrial R&D centre, consists largely of tasks no one chose that trade in order to do. Looking for references. Reformatting data. Writing reports no one will read. Redoing, for the twelfth time, a literature review a colleague has already done in another department. A large share of the professional dissatisfaction in these trades comes precisely from the distance between what one thought one would do and what one does.

A trade reduced to its share of discernment — choosing the questions, arbitrating the leads, deciding what deserves to be tested, interpreting what comes back — is not an impoverished trade. It is a more demanding trade, and it is also, very exactly, the trade most people thought they were choosing.

The problem lies in the path, not in the destination: we are removing the thankless part at the moment when we have built nothing yet to train people in the noble part. There will be a generation caught between the two, and this text has nothing to offer it.

X. What Becomes of Competitive Advantage

One last consequence, for those who have to arbitrate investments.

On what did a research organisation differentiate itself? Historically on three things: access to data or materials others did not have, the presence of exceptional people, and the accumulation of a proprietary know-how hard to replicate.

Let us look at what becomes of each.

Access to public information ceases to differentiate. It differentiated little already; it does not at all now. If the barrier consisted in knowing what has been published, it no longer exists — any competitor can reconstitute a complete state of the art in a few hours. Any strategy that implicitly rests on others not knowing what you know must be re-examined.

Access to proprietary data becomes more differentiating, not less. It is the reverse movement, and it is important. What is not published — your internal results, your failures, your measurements, your production records — becomes the only material others cannot obtain. Its relative value rises mechanically as that of public information falls.

That has an immediate practical consequence on which I shall be brief because it belongs to another debate: an organisation that lets those data leave its perimeter, in whatever form, gives away exactly what remains differentiating about it. That question is handled today by procurement departments, in contractual annexes, with a vocabulary that does not say what it does.

Exceptional people remain differentiating, but not the same ones. The exceptional researcher of the old regime was the one who mastered a body of literature better than anyone. That mastery loses its relative value. The one who keeps it is the one whose quality lies in discernment — knowing what is worth the trouble, sensing what is off, judging rightly. It is a different profile, and nothing guarantees that an organisation which knew how to attract the first knows how to attract the second, nor even that it knows how to recognise it when it has it.

Proprietary know-how splits. The part that was documented in procedures has become easy for a third party to reconstitute. The part that was never written — the part living in hands, habits, the tricks of a workshop or a platform — stays protected by the very fact that it cannot be formalised.

One arrives at a paradoxical result, and I find it the best practical conclusion of this text. When information abounds, competitive advantage takes refuge in exactly what is not information: the data you alone have produced, the judgment of a few people, and physical know-how.

These are three things no technology supplies, that money buys badly, and that organisations have massively under-invested in for twenty years — because they spent those twenty years investing in the processing of information, which was the scarce factor of the previous era.

It is the complete reversal, and it is taking place without being named.

XI. The Loop as Infrastructure

If I had to reduce these four texts to a single recommendation, it would be this one, and it has the drawback of resembling nothing of what is usually presented as a transformation.

Build the arrangement that tells you, two years later, whether you were right.

That is all. No platform, no model, no AI governance: a mechanism that records decisions at the moment they are taken and reopens them at the moment their outcome is known.

I want to defend this recommendation, because it looks derisory beside the sums committed elsewhere and because it is, I believe, the one whose return is highest.

First argument: it is the only thing that makes improvement possible.

An organisation that decides without ever measuring the outcome of its decisions cannot become better at deciding. It can become faster, better documented, more consensual — not better. Improving a competence supposes an error signal, and there is none.

It is a point so obvious that it is almost awkward to write, and yet in practically no research organisation is there an arrangement that systematically compares decisions taken to what they became. Decisions are archived. They are not returned to.

The reason is not technical difficulty. It is that returning to a past decision is socially costly: it names people who were wrong. As long as that cost is perceived as personal, the arrangement will not be built — whatever the declared intentions.

What makes the thing possible is a simple rule that must be laid down from the start: one does not evaluate whether the decision was good, one evaluates whether the reasoning was good. These are two different things and the distinction is decisive. A decision can be excellent and the outcome bad, because the world is uncertain. What one wants to examine is not the result — it is whether the information available at the moment of choice was correctly used.

That distinction is well known in trades where one decides under uncertainty repeatedly, and it is foundational there. It never crossed the door of learned organisations, which judge almost exclusively on the result — which produces two symmetrical perverse effects: luck is rewarded and justified risk is discouraged.

Second argument: it is what turns individual knowledge into a collective asset.

Everything these texts describe — undocumented expert judgment, arbitrations that leave no trace, rejections that go unwritten — comes down to the same thing: an organisation that does not accumulate.

An organisation that does not accumulate starts again with each generation. It therefore rests entirely on the continued presence of the same people, which is exactly the model described at the start of the first text and which we saw no longer holds.

The feedback loop is the mechanism of accumulation. It turns three hundred individual decisions into a body of material one can work on: what are we systematically wrong about, what assumptions do we take for granted without checking, what type of signal do we neglect. None of these questions is accessible without the corpus, and all become so with it.

Third argument: it is what makes it possible to train tomorrow’s judges.

It is the direct link with the problem of transmission. If judgment is acquired through confrontation with error, and if the delay of that confrontation is the limiting factor, then a corpus of past decisions whose outcome is known is a simulator — the only arrangement that compresses into a few months what took years.

The idea is old: it is practised in every discipline that has to train judgment under uncertainty: cases whose outcome is known are replayed, one is asked to decide, then shown. What is missing in research is the raw material: no one has kept the cases.

Fourth argument, and it is the one that should carry a leader’s decision: it is an investment whose cost is low and known.

Recording a decision — the object, the options set aside, the reasoning, the assumptions, what would change one’s mind — represents a few minutes at the moment it is taken. Reopening a batch of decisions that have come due represents half a day per quarter. There is no licence to buy, no platform to deploy, no rare competence to recruit.

Compare that with the cost of the transformation programmes currently being deployed in these organisations, and whose value produced, measured at two years, is very hard to establish.

I see two serious objections and I want to deal with them.

The first: this will work only if people play the game, and they will not.

It is an empirical objection and it is founded. Every arrangement of this type attempted in the form of a compulsory form has failed, for the usual reason: what is perceived as control produces minimal filling-in.

The only configuration in which they have worked, to my knowledge, is the one where the arrangement serves whoever feeds it before it serves the organisation. Concretely: if writing three lines at the moment of a decision makes it possible, eighteen months later, to find instantly why one decided as one did — which everyone looks for regularly and never finds — then the effort is amortised by whoever supplies it.

That is probably, of the whole design, the variable that determines whether the arrangement will live or die within eighteen months.

The second objection: the world changes too fast for past decisions to be instructive.

It is more interesting. If the context has moved so much that a decision from 2023 says nothing about decisions in 2026, then the corpus has no learning value.

I believe that is partly true of the content and false of the structure. Technical facts age fast; modes of erroneous reasoning do not. An organisation that discovers it systematically underestimates regulatory delays, or overestimates the transferability of results obtained on a model, or gives too much weight to the last published result, has learnt something sturdy. These biases are stable, they do not depend on technical content, and they are invisible without a corpus.

That is why I place this recommendation above all the others. It produces nothing visible in the first year. It is the object of no market discourse — no one sells this. It is modest to the point of being disappointing to present to a committee.

And it is the only thing, in all I have described, that I am reasonably certain will have value whatever happens next.

XII. What Could Make All This False

I must now take my own text apart, because a prospective essay that does not is not an essay — it is a brochure.

Here are the four ways this reasoning may prove wrong. They are not stylistic precautions: I believe them genuinely possible, and two of them seem to me more likely than not.

First way: the upstream part may not be as absorbed as I claim.

This whole text rests on the idea that the production of analysis and hypotheses has become almost free. That is true in volume. It may not be true in usable quality.

There is a serious possibility that what is produced at low cost is systematically mediocre in a way one does not detect immediately — plausible, well formed, and slightly off. In which case abundance is not an abundance of usable material: it is an abundance of material that looks usable, which is far more dangerous and far less useful.

The decisive test has not yet taken place. It will take place when one can compare, over several years, the success rate of programmes issued from automated exploration with that of programmes issued from the old method. No organisation collects that data today. It will be available in five years, and it will settle the matter.

Second way: physical time could collapse faster than I believe.

I have built a large part of the reasoning on the irreducibility of validation time. If laboratory automation, simulation and predictive models progress at the rate of the past decade, that irreducibility could shrink to a much narrower portion than today.

In that case the bottleneck would move again — towards the capacity to decide, or towards regulatory validation, or towards acceptability. The general reasoning would hold but its point of application would change, which would invalidate all the practical recommendations.

Third way, and I believe it the most likely: organisations could simply do nothing.

It is the scenario history makes most plausible. The structures described in the second movement have considerable inertia. They are backed by careers, statuses, budgets, professional identities. Nothing guarantees they will evolve because they have become sub-optimal — organisations survive the obsolescence of their design for a very long time, especially when no outside force compels them.

The most likely scenario is therefore perhaps not redesign, but a long period in which AI will be used inside structures conceived for scarcity, producing individual gains, growing queues and no transformation. Ten or fifteen years of tier 1, with flattering dashboards.

If that is what happens, then this text describes what could have happened — which remains useful, but otherwise.

Fourth way: I could be wrong about the question.

It is the most fundamental. I have held that the work of the question would stay human, because present systems answer well and ask badly. That is an observation about the state of the art at a given moment, not a truth of principle.

Nothing establishes that a machine could not, in time, identify a fertile question — spot an anomaly in a corpus, an unresolved contradiction, an assumption everyone takes for granted without its ever having been tested. These are operations one could perfectly well imagine automated, and some work is going in that direction.

If that happens, then scarcity will move again, and it will move towards the only place left: wanting. The decision to take an interest in this rather than that, which is not a cognitive operation but an act of commitment, and which supposes having something to lose.

That is probably where all this ends. But we are far enough from it for that not to be the subject of the next ten years.

XIII. What Will Not Change

After all that precedes, one must name what resists. It matters, because prospective texts have a systematic bias: they overestimate what changes and never speak of what remains.

Matter will not negotiate. That is settled and it is the only solid certainty in this text. Everything that must happen in the physical world will happen at the rhythm of the physical world. An organisation can multiply its ideas by a thousand; it will not make a plant grow faster, nor age an alloy, nor shorten the duration of a cohort follow-up.

Responsibility will remain undivided. Someone will have to sign. The legal reasons could evolve; this one will not: we grant credit only to speech that commits whoever utters it. A recommendation no one answers for becomes a mere suggestion again. That structure is anthropological before being institutional, and it will not move.

Tacit knowledge will remain tacit. Part of what an organisation knows is written nowhere and never will be, because those who hold it do not know they hold it. A fraction of it can be formalised — that is even the substance of what these four texts recommend — but there will remain an irreducible core transmitted by presence and by nothing else. Any organisation that decides to do without long companionship will lose that core, and lose it for good.

Trust will remain costly to establish. An organisation runs on relations between people who have tested one another. No quantity of information replaces having worked together on something difficult. That capital constitutes itself slowly, is destroyed fast, and has no technological substitute.

And finally, the difficulty of changing will remain the same. It is perhaps the most useful remark in this text for a leader. Nothing that precedes belongs to technology; everything belongs to organisational decisions that run into interests, statuses and habits. Technology has accelerated by several orders of magnitude. The capacity of organisations to reform themselves has not moved an inch, and it is probably that, in the end, which will determine who comes through this period and who does not.

XIV. The Question That Remains

I should like to finish on what seems to me the most interesting consequence of all this, and it is not the expected one.

Much has been said about artificial intelligence democratising knowledge — that everyone would have access to what was accessible only to a few. That is true, and it is probably good news.

But what this abundance reveals is more disturbing. When everyone has access to all the answers, what distinguishes organisations is no longer what they know. It is what they look for.

And that is precisely the thing no one has ever attended to. We have built extraordinarily sophisticated institutions for producing and validating answers — universities, journals, laboratories, committees, protocols, peer systems. We have built rigorously no institution for producing good questions. They have always been the doing of individuals, often solitary, and generally ill understood by the structures that employed them.

That did not matter as long as answers were scarce. The scarcity of answers acted as a selection: a badly put question cost only the person who put it, since it took years to discover that it led nowhere, and that cost fell on them alone.

Now that answers are abundant, a badly put question costs everyone — because it instantly mobilises a considerable production capacity, because it produces a mass of convincing material, and because it occupies the queue ahead of those that deserved to be in it.

That is why I believe the coming decade will turn, in learned organisations, on something very unexpected. Not on the power of the models, nor on the quality of the data, nor on AI governance.

On the capacity to decide what deserves to be looked for.

It is work we have never organised, that we do not know how to evaluate, for which we train no one, and which has a holder nowhere.

It has just become the only work that counts.

I should like to leave a last image, because it has served me more often than an argument.

A research organisation long resembled a marksman with few rounds. All its art lay in aiming: judging the distance, correcting for the wind, taking its time. The institutions it gave itself — the committees, the files, the feasibility reviews — are devices for aiming. They were built because every shot was expensive.

What has just happened is that the rounds have become free. Not the targets: they are still as far away, as hard to hit, and there are no more of them than before.

The instinctive reaction is to shoot more. That is what most organisations do today, and it is what their indicators encourage them to do, since the number of shots is what they measure.

The right reaction is different. When shooting costs nothing, the question is no longer how to aim. It is: what are we shooting at, and who chose those targets?

No one has ever had to answer, because the cost of the rounds answered in our place. An organisation that could shoot only three times had no need of a doctrine for choosing targets: it took the three most obvious, and that was rational.

It is that economy of decision that has just disappeared, and it carries away with it a great part of what we thought we knew about how to organise research.

I do not know what will replace it. I think I know where one will have to look, and it is not on the side of the models.