The Half That Does Not Speed Up

Essay III

The Half That Does Not Speed Up

On the economics of two-speed organisations

I. The Wall

A research team shows me, with legitimate pride, what it has obtained over the past year.

Previously, framing a serious hypothesis, the kind that justifies setting up an experiment, took several weeks. One had to read, cross-check, discuss, discard. Today, with the tools at its disposal, the team produces one every working day. Documented, argued, referenced, plausible.

Two hundred and forty hypotheses in the year, where there had been twenty, a year or two earlier. I ask how many they have tested. Silence, then the answer. Eighteen. Roughly what they were testing before. And roughly what they will test next year, and very probably the year after.

I then ask the question one forgets. What does one of those eighteen tests cost, and who set the number. Eighteen may be a capacity ceiling. It may also be a budget line that gets renewed without being reopened. The first case is the one this text describes. The second is a portfolio-steering failure, and a budget exercise corrects it.

Two hundred and forty hypotheses. Eighteen tests. The rest waits, in a file no one reopens, and which grows. One half of the organisation has just accelerated by a factor of ten, and the other half has not moved a hair.

This asymmetry is a fact, and it is missing from almost every conversation about artificial intelligence. There is talk of productivity, adoption, time saved, use cases. There is rarely talk of what happens when one accelerates a single side of a system that has two.

It is not accelerated. A queue is built.

A queue is an economic object, with laws of its own. It destroys value, and it shifts where an organisation should invest.

II. Two Clocks

Every research organisation runs on two clocks that have no relation to one another.

The first is the clock of thought. Framing a question, looking for what exists, building a hypothesis, designing a protocol, interpreting a result, writing a recommendation. This clock is set by people’s cognitive availability. It is slow because people are few and busy.

The second is the clock of matter. Growing a plant. Carrying a patient cohort to an endpoint. Ageing a material. Waiting for a season, a reproductive cycle, a latency period. Obtaining a committee’s authorisation. Running a pilot trial. This second clock is set by something other than us. Biology, chemistry.

The distinction looks trivial. Our expert organisations were built as if the two clocks ran at roughly the same speed.

That was true in part of the sciences and false in the other. At a chemistry bench, designing an experiment took a few weeks and running it took a few months, a ratio of one to three, sometimes one to five. In plant breeding, forestry, cohort epidemiology, the ratio was one to a hundred before any machine got involved, and it already was in the nineteen-seventies.

Those houses did not discover the asymmetry with artificial intelligence. They built their staggered pipelines, their overlapping generations, their off-season nurseries and their portfolios staggered by a year precisely to live with a ratio of one to a hundred.

What has changed is the amplitude, and the fact that these structures were all calibrated on a given upstream flow. A pipeline designed for a hundred hypotheses a year absorbs a hundred and twenty without flinching. It does not absorb a thousand. The ratio of one to three has become one to thirty. The one of one to a hundred has moved in the same proportion.

The clock of matter is not completely rigid, that is the serious objection to this text, and it will come. The compression of physical time is not uniform. It reaches an order of magnitude where the experiment can be parallelised or replaced by a calculation. It caps at a few tens of per cent where the duration of the trial is the phenomenon itself. The compression of design time, for its part, has been several hundred per cent, everywhere at once, with no distinction of field.

The cost asymmetry has narrowed too. An off-season nursery is rented by the plot from a provider. A sequencing or phenotyping slot is bought by the unit like a dosage. A study is subcontracted to a contract research organisation. A growing share of experimental capacity has become operating expenditure, purchasable at the margin, with no capital tie-up or equipment lead time. Upstream compression has been general and fast. Downstream compression stays uneven, it is paid for, and it stops where time is the phenomenon.

These are two different orders of magnitude. Many investment strategies still ignore this and go on funding massively the side that has just become abundant.

III. The Queue

The spontaneous intuition is that a queue is a stock that waits, and that a stock that waits is neutral. It produces nothing, it destroys nothing either, and it will be dealt with later, in order. That is false on three points, and each error costs money.

First point, the contents of a queue go stale.

A hypothesis framed today rests on today’s state of knowledge. Eighteen months later, part of what founded it has moved. A result published elsewhere, a patent filed, a regulatory change, a shift in the market. The queue therefore contains hypotheses that were good and no longer are, and no one knows it, because no one re-examines a queue.

The rate of staleness is not marginal. In fields where the literature moves fast, a good share of what waits more than a year has lost most of its interest. The organisation paid to produce those hypotheses. It will never test them.

Second point, a long queue makes ordering decisive, and ordering rarely exists.

When twenty hypotheses wait for eighteen places, order matters little, almost everything will get done. When two hundred and forty hypotheses wait for eighteen places, order is the thing that counts. The value produced in the year depends on the quality of the sorting.

And that sorting was never designed as a function. It has no holder, no written criteria, no budget, no evaluation. It happens through mechanisms that were acceptable when little was at stake. The seniority of the requester, insistence, closeness to the decision-maker, order of arrival, familiarity with the subject.

Third point, and it is a repeated impression rather than a measurement. A long queue discourages the production of quality.

It is a behavioural effect. When a researcher knows their hypothesis has one chance in thirteen of being tested, and that this chance depends on factors they do not control, they stop investing in the quality of their hypotheses. They produce more of them, which raises their statistical odds, and they take less care over them. The system rewards volume.

This third effect therefore depends on the second. It supposes the sorting stays opaque, and it reverses the day the criteria are written down and published.

One therefore obtains, mechanically, a queue that lengthens and whose average quality falls. Which makes the sorting both more important and more difficult.

The result is a situation I believe fairly widespread today. An organisation that has invested heavily in its capacity to produce ideas, that observes an explosion of upstream activity, and whose production of results is rigorously identical to what it was before.

It does not understand why. It often concludes that the problem lies in execution, that more experimental capacity is needed, more equipment. It asks for budgets to widen the bottleneck. The answer is understandable, and often wrong.

IV. The Science of Waiting

There is a science of waiting. It is not new, having been built in 1909 to size Copenhagen’s telephone exchanges, then applied to factories, then to hospitals. It says precise things about what happens when a limited capacity receives a flow that exceeds it. Three of its lessons apply directly here.

The first, waiting does not increase in proportion to load. It explodes.

As long as a system runs at sixty or seventy per cent of its capacity, waiting times stay moderate and roughly predictable. Beyond eighty-five per cent, they take off, and variability takes off with them. The curve is an asymptote.

Most research organisations were already running, before AI, at high load rates, because leaving experimental capacity unused is regarded as a management fault. They were living near the asymptote. What happened next is of a different nature. Two hundred and forty arrivals for eighteen slots make a ratio of thirteen, and the system has crossed to the other side of the point of stability. There is no longer an asymptote because there is no longer any steady state at all. The stock grows, steadily, indefinitely, at the pace of the difference between what comes in and what goes out.

The second, adding capacity is expensive and relieves little.

Near saturation, adding ten per cent of capacity reduces waiting by far more than ten per cent, because you leave the asymptotic zone. It is the best return known to queueing theory. An incoming flow multiplied by twelve is not caught up with that way. Experimental capacity would have to be multiplied by twelve, which is neither fundable nor physically possible in most fields.

It is then necessary to say precisely what capacity buys and what it does not buy. One more experimental slot shortens no delay. The eighteen programmes already under way advance at the same pace, whether they have two hundred hypotheses behind them or twenty. What it buys is one more tested hypothesis, the nineteenth by order of merit, and its return grows with the length of the queue, since the pool one draws from has grown richer. That return is real and it can be calculated. Where capacity is rented, by the plot or by the sequencing slot, the arbitration is posed slot by slot, cost of the slot against the value of the hypothesis one gives up.

What capacity will never buy is order. One more slot moves eighteen to nineteen. A better sorting acts on all eighteen at once. That is a difference of reach, and it is this, rather than a saturation argument, that puts sorting ahead of capacity when both cost the same.

The third, when capacity cannot be increased, the only remaining variable is the quality of the input.

A saturated system is treated by three routes. The incoming flow is reduced. The selection of what enters is improved. The third reduces variability, both of arrivals and of trial durations, through batched campaigns and fixed lot sizes. It is the cheapest of the three and it is too often forgotten. It has a limit. At a ratio of thirteen between what enters and what leaves, smoothing arrivals changes nothing. It serves those living near saturation, not those who have crossed it.

In an organisation saturated downstream, value is no longer created in production. It is created in the sorting.

Sorting becomes the only thing that determines performance. Two organisations producing the same number of hypotheses, with the same experimental capacity, differing only in the quality of their selection, will obtain results beyond comparison, because one will have tested its eighteen best hypotheses and the other eighteen arbitrary ones out of two hundred and forty.

That gap has an upper limit, of course. The gain from a sorting is the difference between the expectation of the eighteen best under the criterion one has and the expectation of eighteen taken at random. That difference is zero if the criterion says nothing about quality, and it reaches its maximum if the criterion predicts it perfectly. It therefore depends on a quantity no one measures, the share, visible before the test, of what will decide a hypothesis’s success. If it is half, sorting is the only subject that matters. If it is five per cent, it is worth building and it will overturn nothing.

It is a strong economic argument in favour of everything that touches evaluation and judgment. Queueing theory supplies only a premise here, and it is arithmetical. Two hundred and forty enter, eighteen leave. Everything else is order statistics. When only a fraction of a pool can be served, what determines the result is the rule that decides the rank.

V. The Wrong Indicator

Almost every research organisation tracks the same figure, the number of experiments run. It goes by various names, experimental throughput, number of trials, campaign volume, platform occupancy rate. It was long a good indicator. When experimental capacity is the limiting factor and ideas are scarce, running the machines at full is what should be done.

That figure today measures the wrong thing, and it measures it all the worse for being good.

Consider two teams. The first runs a hundred and eighty experiments in the year, of which twenty confirm the hypothesis tested. The second runs a hundred and twenty, of which forty confirm.

On the throughput indicator, the first is clearly better, with fifty per cent more activity. On the confirmation rate, the proportion of experiments whose result validates the opening hypothesis, it is three times worse. What that gap means depends on information the indicator does not give. Did the first team’s hundred and sixty unconfirmed experiments produce written, reusable exclusion boundaries, or did they close on a finding no one will ever reread? In the first case, it manufactured a great deal of knowledge. In the second, it spent more to leave less behind. An indicator that counts a properly instrumented failure as zero measures compliance and nothing else. The one I propose must count both.

For a long time, there was no need for it. When hypotheses were rare and dearly acquired, they were all carefully built, and the confirmation rate varied little from one team to another. An indicator that does not vary carries no information: it is not collected.

It is also ambiguous. A very high confirmation rate is a bad sign: it indicates that only what one is already sure of is being tested, that is, that one is not exploring. A very low rate indicates shooting in the dark. There is an optimal zone, it depends on the field, and determining where it lies requires work no one has done.

But the real reason is political. The confirmation rate evaluates the quality of the judgment of whoever proposed the hypothesis. It is therefore opposable to those who yield it. It is the type of measure that an expert organisation refuses to give itself, as seen elsewhere, because it makes explicit a hierarchy of discernment one prefers to leave implicit.

I believe that it is this indicator, or a close relative, that will determine the performance of research organisations in the next ten years. It is imperfect. It is also the only one that measures the factor that has become limiting.

There is a simple test for knowing whether your organisation is looking in the right place. Take your R&D dashboard. Count the indicators that measure volume, number of projects, trials, publications, filings, use cases, users. Count those that measure correctness, confirmation rate, rate of decisions not revised, proportion of stopped programmes that should have been stopped earlier.

The ratio is almost always at least ten to one in favour of volume. Often, the second column is empty.

It is the exact reflection of what these organisations knew how to measure at the time their dashboards were designed.

VI. The Material Clock Is Accelerating Too

The strongest objection to what precedes rests on facts in progress.

The clock of matter is accelerating too.

Automated laboratories today make it possible to run series of experiments with minimal human intervention and a throughput that has nothing to do with manual work. High-throughput screening tests tens of thousands of conditions where a few dozen used to be tested. Numerical simulation replaces a growing share of physical experimentation, in computational chemistry, structural mechanics, materials modelling, protein folding prediction. Miniaturised sensors and automated imaging have collapsed the cost of phenotyping in several biological fields.

In some sectors, the compression of experimental time over the past decade is an order of magnitude.

The objection establishes that parts of the material clock are accelerating, not all of them, and not the same ones from one field to the next.

What accelerates is what can be parallelised or simulated. If the experiment is short and a thousand can be run at once, automation changes everything. If the phenomenon is described well enough by a model, simulation replaces it.

There is a third route, stronger than the other two and rarely named alongside them. One stops having to run the trial at all. An early criterion correlated with the final one replaces it for the vast majority of candidates, and only the small surviving batch is carried through to the end. Genomic selection is the most documented case. It reduces the number of field trials by substituting a marker-based prediction for entire generations of phenotyping, and across several major species the breeding cycle has been cut by half or a third in twenty years. Clinical medicine does the same with its surrogate endpoints and interim analyses. Choosing the criterion is an act of experimental design, and it is by far the most profitable one.

What does not accelerate is what rests on an irreducible development time or on external validation. A clinical cohort must be followed for the period its protocol provides. A material put through accelerated ageing gives an indication, and approval will require the real ageing. A regulatory file waits behind others before an authority whose capacity does not depend on you. I long filed the biological reproductive cycle under this category, and it is the worst example I could have chosen. A generation has never been shortened by a single day, and the breeding cycle has been cut by half or a third, because one stopped waiting for every generation.

Trials can be multiplied in parallel. One cannot shorten the time of a trial whose duration is the phenomenon itself.

That is why I believe the objection displaces the problem without removing it. Where matter accelerates, the bottleneck moves towards the final validation, the one that stays slow, and which becomes all the more critical for being the only point where reality still has a right to speak. An organisation that tests ten thousand hypotheses in simulation will still have to validate a few dozen in the real world, and the sorting that decides which ones is exactly the problem described above, with a worse scale factor.

These fields run a particular risk. When the upstream and part of the downstream accelerate together, one can run a wholly self-referential system for a very long time, hypotheses generated by model, validated by simulation, feeding other hypotheses, without ever touching the real. The system produces an impressive quantity of apparent knowledge, and it can drift for months before anyone notices, because the point of contact with matter has become so rare that it no longer corrects anything.

A second objection, more down to earth. If the problem is the queue, let us reduce the incoming flow.

Two things are always conflated here. Curbing the production of ideas supposes deciding upstream what deserves to be framed, that is, exercising exactly the judgment one does not have. And it sacrifices what is genuinely precious in abundance, the possibility of exploring directions one would never have explored, because they were not worth three weeks of work but are certainly worth a day.

Capping admission is another matter. Nothing enters the experimental queue until something leaves it. It is the factory kanban, which will come up again later. It counts, without judging anything. One can explore two hundred and forty directions in the year and admit only twenty at the border between the two clocks. The benefit of abundance stays whole. The cap costs one governance decision and nothing else.

A cap fixes how many enter. It never says which. When a slot frees up and two hundred candidates are waiting, a choice must still be made, and a cap with no criterion chooses by order of arrival, that is, by one of the failing mechanisms ranked above. The cap shifts the queue one notch upstream and makes its cost visible. It makes the sorting compulsory and datable.

VII. The Internal Fracture

A two-speed organisation very quickly becomes a problem of people. It is the dimension that reaches leaders last.

Take the configuration described at the start of this text. On one side, a team producing hypotheses at a rate it had never known, which feels effective, which sees its work transformed. On the other, a team that executes, whose rhythm has not changed, and which receives growing pressure from upstream.

What the upstream feels, enthusiasm, then frustration. Good work is produced and comes to nothing. One ends up attributing the blockage to those who execute. Too slow, too attached to their procedures.

What the downstream feels, illegitimate pressure. You are asked to absorb a multiplied flow with no extra means, with requests more numerous, more insistent, often less well prepared than before, because producing a request now costs ten minutes. And you are reproached for your slowness when nothing in your work has changed except the number of people waiting on you.

Both are right, which makes the conflict insoluble at their level.

This conflict is structural, and it is nearly always misunderstood. It is generally read as an opposition between profiles, the modern and the conservative, those who took the turn and those who resist. That reading is comfortable because it names culprits and suggests a simple solution, support the change and convince.

It is false. You can replace the downstream team entirely with enthusiastic and perfectly trained people, throughput will not move, because it is determined by physical time and not by state of mind. The conflict will reappear identically in six months with new people.

A side effect makes everything worse, the perceived relative value of the two halves.

The upstream side is the one that shows itself. It produces documents and feeds committees. Its activity is visible and it has doubled. The downstream side is the one that executes, whose work is not very narrative, and whose activity has not moved.

Before an executive committee, these two realities do not carry the same weight. The upstream looks dynamic, the downstream looks static. Budget arbitrations follow. More for those who move, more for the tools that produce visible results, less for the experimental capacity whose failure to keep up no one understands.

So the side that is not the bottleneck is funded by taking from the side that is. It is the worst possible arbitration, and it is produced by the very structure of what leaders observe. A slower and graver consequence follows, on the people themselves.

The best profiles on the downstream side are exactly those whose value rises under the new regime, since they carry a competence that does not replicate. Those who know how to set up a clean experiment, and who know before having launched it that such-and-such a protocol will give an uninterpretable result. They are also those who receive the clearest signal that their trade is regarded as the slow and uninteresting part of the chain.

They leave. Not all, not at once, but the correlation between quality and departure is strong in these situations because the best have options. And the organisation finds two years later that its capacity to execute has degraded, without making the connection with the way it distributed its investment and its attention.

The only thing that works, to my knowledge, is to make the constraint visible and shared. Display the same figure before both halves, rather than explaining to people that they should understand one another better. Here is the number of hypotheses produced this quarter, here is the number tested, here is the ratio. When that ratio is before everyone’s eyes, the conversation changes in nature. The upstream stops being against the downstream, and an organisation looks together at an imbalance.

It is also the only way to make the upstream understand that producing more does not help. No speech manages to establish it, and a figure establishes it in one meeting.

That supposes measuring the ratio. Almost no one measures it. It is an indicator that costs a few hours to build and is worth, wherever it is adopted, every alignment seminar there is.

VIII. Industry Has Already Solved This Problem

The problem described here was identified and solved forty years ago, in factories. It is a little frustrating.

The history contains both the solution and the reason research never applied it to itself.

In the nineteen-seventies and eighties, Western industry ran on a principle that seemed obvious, maximise the use of every machine. An idle piece of equipment was sleeping capital, and a workshop’s performance was measured by its occupancy rate. Each station produced as much as it could, and what it produced piled up in front of the next one.

The result was factories full of work in progress, with interminable and unpredictable lead times, quality that degraded because defects were detected only very late, and cash tied up in intermediate stocks no one counted as a cost.

Two currents took that reasoning apart, at roughly the same time and by different routes.

The first, Japanese, is the Toyota Production System formalised by Taiichi Ohno. It established that an intermediate stock is a symptom rather than an asset, and that it masks all the system’s problems. The answer consisted in deliberately reducing stocks to make the malfunctions appear, then in producing only at the request of the downstream station, completely reversing the direction of the flow.

The second is the theory of constraints, which states something more drastic still. In every system there is a bottleneck, and any improvement that does not bear on that bottleneck has no effect on overall performance. Improving a non-constrained station only piles up more work in progress in front of the bottleneck. It is wasted work, if not harmful work.

The practical conclusion was counter-intuitive and took twenty years to impose itself. Everything that is not the bottleneck must deliberately be under-used. An upstream station running at sixty per cent is at its correct setting.

Now look at what a research organisation does when it deploys AI massively on its upstream.

It increases the throughput of a non-constrained station. It piles up work in progress in front of the bottleneck. It measures its performance by the occupancy rate of its resources rather than by output flow. And it reads the accumulation as a sign of vitality.

It is exactly the factory of 1975.

These principles, applied for a long time in production, logistics, services and even software development, never crossed the door of laboratories.

Three explanations.

Research has always thought of itself as a trade of creation rather than of flow. Speaking of bottlenecks, work in progress and throughput about an activity of discovery seems reductive, and that semantic resistance was enough to set aside a whole body of operational knowledge. It was preferred to consider that these categories did not apply rather than to examine whether they did.

The bottleneck, next, was not visible. In a workshop, work in progress is a heap of parts in front of a machine. It is seen, it physically gets in the way. In a house of knowledge, work in progress is a file. It gets in no one’s way, and it can grow indefinitely without ever causing the discomfort that triggers action.

And the constraint moved. In a factory, the bottleneck is stable and locatable. In research, it changes position according to projects and phases. That variability served as an argument for not seeking to identify it, when it made identification more necessary still.

One must however name what does not work in the transfer. A factory knows what it produces, the value of a conforming part is known in advance. A research organisation does not know what its output is worth before having produced it, and often long afterwards. The whole logic of pull flow supposes an identifiable downstream demand, and here demand is a hypothesis about the future.

That difference is real and it does not invalidate the central principle, which does not depend on knowing the value. Improving what is not the bottleneck improves nothing. That proposition is true whatever you produce.

IX. The Other Queues

I have concentrated on the experimental queue because it is the most visible. It is not the only one, and the others are probably worse, because they are not even counted.

The queue of decisions. An organisation can arbitrate only a limited number of subjects per period, and that number is determined by the availability of its bodies, committees and boards. These bodies have a fixed capacity, set by the calendar and by the time of people who are themselves scarce.

AI has not increased that capacity. It has on the other hand considerably increased the number of subjects that come up, and the size of the files that accompany them. The same committee, with the same duration, has to handle more subjects, better documented. So it handles them less well, or it postpones, and the queue of decisions lengthens exactly like the other, with the same staleness effect and the same degradation of the sorting.

It is a queue whose length no one measures, because a subject not put on the agenda appears nowhere.

The queue of validation. We have spoken of it elsewhere, checking has become more costly than producing. Any organisation that increases its production without increasing its capacity to check builds a queue of unchecked things, and that queue has a formidable peculiarity. It is invisible even to those who constitute it, because nothing outwardly distinguishes a checked document from one that has not been.

The regulatory queue. In every sector subject to authorisation, the authority’s processing capacity is an external constant. It does not adjust to your productivity. A whole industry accelerating its upstream simultaneously only lengthens the queue in front of the same counter, and the average delay lengthens for everyone. Each one’s gain becomes everyone’s loss.

And finally the queue of attention. It is the most general, and it is the one all the others depend on. The number of subjects an organisation can bring real attention to, understand a question and form a conviction about it rather than tick a box, is narrow.

All these queues have the same structure. All receive a flow that has been multiplied. None has seen its capacity increase. And none is measured.

AI has been presented as a technology that increases the capacity of organisations. I believe it can also do the opposite, increase the flow and leave capacity unchanged. It multiplies what enters the system. It does not touch what the system can absorb, because that capacity is made of physical time, availability of attention and capacity to decide.

An organisation that does not understand this will invest massively to increase a flow it already cannot handle, and will call that a transformation.

X. Where to Put the Money

First consequence, stop investing in the capacity to produce ideas. It has become abundant. Every additional euro spent on producing more hypotheses, syntheses, proposals and files lengthens a queue that is already unmanageable.

Yet that is where the bulk of AI budgets in R&D goes today, because that is where the gains are easiest to demonstrate.

The stock, for its part, is not free to carry. It goes stale, at the rate seen above. Each additional candidate consumes a little of the attention the previous section made the hardest queue to loosen, and reading then comparing before discarding is paid for in the time of scarce people. Out of two hundred and forty hypotheses, a few will look promising by pure chance, which manufactures apparent reasons to test. None of these three costs is measured anywhere. Even if they were nil, the recommendation would hold. One stops paying for a marginal benefit that no longer is one.

Second consequence, investment in experimental capacity must be arbitrated differently. The question that matters now is that of the irreducible bottleneck. In fields where experimentation is parallelisable, investment in automation keeps all its sense and is probably under-scaled. In fields where physical time is irreducible, increasing capacity only increases the number of simultaneous experiments without reducing the delay, which may be useful but does not solve the problem posed. Confusing the two situations leads to funding equipment that will change nothing.

Third consequence, perhaps the main one. The only high-return investment today bears on the sorting. On the criteria that determine what gets through. On the people who apply them. On the mechanisms that make it possible to know, after the fact, whether the choices were good. On the memory of past decisions, which is the only raw material for improving the sorting.

It is a modest investment in euros and a considerable one in organisational difficulty. It cannot be bought or subcontracted. It produces no visible result for several months. And it runs into the resistances already described, since it amounts to making explicit the quality of the judgment of people who have always had the right not to justify it. That is why it is almost never made, although its return is by far the highest.

Fourth consequence, more uncomfortable. Part of the queue must be destroyed. An organisation producing two hundred and forty hypotheses a year and testing only eighteen also accumulates a moral debt to those who produced them. Each represents someone’s work, and the queue functions as a tacit promise that one will come back to it some day.

One will not come back to it. Better to say so and purge, rather than let a hundred people believe their work is waiting when it is dead. The cost of an announced purge is a disagreeable moment. The cost of a phantom queue is the slow demotivation of everyone who feeds something they eventually understand serves no purpose.

XI. The Question to Ask

One operation you can carry out this week is enough to settle it.

Take the number of hypotheses, proposals, leads framed in your R&D last year. Take the number of those actually tested, developed or carried through to a decision.

Take the ratio. Then take the same ratio for the year 2019.

If that ratio has been divided by five or by ten while the number of hypotheses framed exploded, then you have not transformed your R&D. You have accelerated the half that was not the bottleneck, and you have transferred the whole problem onto the half that was.

A house that carries three hundred leads through to a decision and funds only ten passes this test without difficulty. The test counts what is settled, funded or not, and concluding there is no interest is a decision like any other.

Nothing in that is a failure, the stage is even normal. It is logical that acceleration should arrive first where it is technically possible. What would be a failure is not seeing that the point of application of the effort must now change completely.

The question that matters, for a leader, is what, in their own house, cannot accelerate. That is where the value now lies, and no one is looking there.