Working notes on the role of vision papers in basic science

By Michael Nielsen
May 28, 2022

Many of the papers I most admire are vision papers1. Rather than abstractly define what a vision paper is, here's a list of a few examples of such papers, to convey the gist:

There are many more such vision papers; a few are listed in the footnotes2. But hopefully you get the idea. Most vision papers quickly fade into obscurity. But the most successful often play crucial roles in pioneering new fields, including computer science, geoengineering, gravitational wave astronomy, genomics, and many others.

(I will resist the urge to more precisely define what is meant by "vision paper". Premature definition is the root of much bad creative work. It seems more useful, at this early point, to explore the broad genre of "things like the above list" – collecting examples of vision papers, trying to understand what they do, and the role they play, differences in approach, differences and similarities to conventional papers. Such detailed work is, of course, the grist out of which good definitions may eventually come. In this case it seems likely to always be shades of grey; far more useful than categorization is understanding the detailed mechanics. My apologies to any readers frustrated by this lack of definition.)

The immediate motivator for the present notes is a combination of observations I find surprising: (a) vision papers often play a crucial role in instigating new fields of science; and yet (b) the kind of thinking they involve is of a type that scientists often don't publicly do much of; indeed (c) the style of thinking involved is sometimes disparaged by many (not all) scientists. Often, the papers contain few or no technical results, and little or no data. They may, in fact, not hew to the usual standards of any existing field. As a consequence, the contents of vision papers tend to be radically different than most conventional scientific papers. They're often storytelling or narrative creation, with few technical results, and sometimes apppear superficially closer to literature than what people ordinarily consider science.

When vision papers are published, they're often ignored; they're certainly rarely much respected. Several people who work fulltime (today) on quantum computing, told me in the 1990s that the founding papers of the field were vague and wishy-washy, "not real physics". It took time for those fundamental papers to become celebrated. This is a common pattern: many important vision papers are ignored early, with success coming much later, if at all.

This all seems like a curious combination. What's going on? When are these papers valuable (or not)? If it's true that vision papers sometimes play a crucial role in science, then is it a bad thing they may be regarded negatively? Indeed: why are they regarded negatively? With Kanjun Qiu, I've been wondering: would there be any benefits to soliciting visions, perhaps as part of some kind of Vision Prize competition? Would it be possible to speed up the creation of new fields of science this way? And then there's personal questions, as well: is it useful to develop this style of thinking? What role should it play in one's own work? And part of me shares the instinctive aversion to vision papers I mentioned above; indeed, I sometimes feel a little sheepish about vision papers I've written. At the same time, this feeling of sheepishness seems utterly bonkers.

The purpose of these notes is to engage these questions. I must admit: I'm a little embarassed to be writing the notes! It feels like so much faffing around, visions-of-visions, like blogging about blogging. But those concerns are wrong. Vision papers are connected to fundamental questions like the way scientific fields are founded. And they're interesting as a distinct kind of epistemological object, something that no-one, as far as I know, has ever thought about as a particular type of knowledge. They're worth understanding better.

Throat-clearing aside, let's get back to the subject. I've asserted writing vision papers is often regarded as lightweight. It's difficult to prove this. I've certainly heard scientists say negative things about such work; occasionally the comments are scathing. More often, such work is ignored, or regarded as "fun speculation, but not real science". There are few venues for such work. I'm certain the median number of vision papers in an issue of Physical Review Letters is zero3.

One striking illustration of how unusual vision papers can be is provided by one of my favorite examples in the genre, Alan Kay's 1972 paper "A Personal Computer for Children of All Ages". This paper is perhaps most often described as inspiring parts of the iPad design – a worthy achievement, but the paper is deeper than that description suggests4.

One striking thing about the paper is the things it doesn't do. It doesn't describe any real computer system, not even a (digital) prototype. It contains no code, no theorems, and little or no evidence or ideas or arguments or data as they are usually construed in computer science (or any other field of science). In other words, it contains arguably no scientific results of any recognized kind. It's more a story or a series of sketches, trying to evoke possibility, through a back-and-forth between the sketches, fundamental questions, and stimulating interconnections between fields. Despite that highly non-standard form, it's a beautiful paper, one with astonishing depth of insight, and which has directly influenced much of my creative work, and the creative work of others.

Contrast this with a very different vision paper, also extraordinary: Fault-tolerant quantum computation by anyons, by Alexei Kitaev.

Unlike Kay's paper, Kitaev's paper is a technical tour de force. He develops a new class of quantum error-correcting codes; connects them to the properties of certain condensed matter systems; and outlines many of the technical ideas needed to make a novel state of matter which naturally performs quantum computation. It's worth restating that last for emphasis: Kitaev is pointing the way toward a state of matter which naturally quantum computes. This is an incredible idea.

Kitaev's paper is both an astonishing set of technical results, and – quite independently – an astonishing vision, one radically contradicting almost all prior intuitions about the way the universe works.

This description may perhaps be taken as an implicit criticism of Kay's paper, and praise for Kitaev's. That's not the point. Quite the reverse: the point is that whether a vision paper is successful seems surprisingly independent of the strength of the technical results contained therein.

In normal science5, a good paper contributes some brick or bricks in the edifice of knowledge. Maybe it's an enormous contribution – Wiles' proof of Fermat's last theorem, for instance. Or maybe it's something tiny – a chemist measuring the solubility of some substance under conditions no-one had ever previously gotten around to measuring under. While less important, it shares in common with Wiles that it is something other people can build upon. It's something (provisionally) true about the world, usually expanding in a tiny way what we can do or predict or understand about very specific actions in the world.

By contrast, the key element of a vision paper isn't a new fact about the world. It's effectively a would-be prophet standing up and proclaiming: "I see a wonderful opportunity over there, that looks [something like this]. Let's go explore!" Kay's is a vision of new media transforming the way people learn and think. Kitaev's is a vision of materials with properties so radically different to the ordinary world that they would make an invisibility cloak seems mundane.

A good vision paper reveals and evokes an exciting latent possibility, without necessarily saying concretely how that possibility is to be achieved. Indeed, it may not even necessarily lay out a concrete goal, much less concrete steps to achieve it. But there is a direction, and a plausible exciting latent possibility.

Often, no-one pays any attention to such visions, or only a few people pay attention. But sometimes a large number of people head off in the direction, albeit often after considerable delay. In the two examples I've just been using, both Kay's and Kitaev's papers developed visions that (eventually) inspired quite a few people to explore6.

Visionary versus composable results: I made a distinction above between the detailed technical results in a paper, and the "visionary" aspects. I claimed Kay's paper was mostly visionary, while Kitaev mixed both; indeed, much of the vision in Kitaev was implicit.

I've struggled to articulate the difference between the technical and visionary aspects. In part, it's because the line is genuinely blurry. However, roughly speaking: technical results are things about the world that others can build upon; they are in some sense composable. You can take Fermat's last theorem or a measurement of solubility and use it to do other things. In Kitaev's case: he explicitly constructs a class of error-correcting codes: you can use those constructions to do other things. Kitaev describes a class of condensed matter systems: you can try to build those systems, you can study their properties, you can try variations. And so on: there are many strong technical results in Kitaev's paper, things which can be directly built upon.

By contrast, the visionary aspects don't have this composable nature. They're stories7: "Here is an [exciting, non obvious latent opportunity] which [you could help move toward]. That movement perhaps looks [something like this], and [may involve these ideas, often pre-existing or drawn from other sources]." The idea of a state of matter which naturally quantum computes is a very exciting idea, but there's nothing you can directly do with that idea. You can't directly build on it, unlike (say) the error-correcting codes in Kitaev's paper. Rather, it's a motivator.

I'm struggling to state this demarcation satisfactorily! Let me try once more: the technical, composable aspects of a paper directly affect what we can do in the world, or what we can do with our theories of the world. They make a lasting contribution to human capability, to what we understand or can do. The visionary aspects instead affect what scientists think about, what they think is important, what opportunities they recognize as worth moving toward. But they're not primarily reused as components in other work8.

Of course, Kay's vision paper was followed up by lots of conventional technical progress – by the development of Smalltalk and the Alto computer (which then influenced computers like the Apple Macintosh) and many crucial ideas about programming environments, interfaces, and computer systems. Without that technical follow up, the paper would have faded into obscurity.

Many striking visions aren't ever backed up by technical progress in this way. There's a book by J. Storrs Hall which has been widely read in Silicon Valley recently, Where is My Flying Car? It's an interesting book, describing a number of apparently plausible visions, which seem to have stalled out. There's a standard laundry list of things to blame for this stall: the most common are a general stagnation or Gibbonesque malaise in culture or individual will; and sclerotic, risk-averse scientific institutions.

I have both considerable sympathy for and considerable disagreement with these explanations. But there's an entirely different explanation which is not often said publicly: the visions often stall because the people proposing them lack either the will or the ability to take technical steps toward them. When that's the case it's unsurprising other scientists don't pay much attention. If the originator of the vision doesn't have the technical wherewhithall to make progress, it's reasonable to wonder if perhaps they didn't understand things as well as they thought. And so other people don't come onboard, and the vision fades.

This story would be much stronger with concrete examples. I certainly have some in mind, but I won't give them, since it's pretty rude (and potentially hurtful) to say someone's contributions are technically weak.

However, there's one example I am comfortable using: my own essay Toward an Exploratory Medium for Mathematics. This is an example of a failed vision, or – more generously (and, I fondly hope, more accurately) – of a vision whose time hasn't yet come. And I suspect the main reason is simply that I didn't push hard enough technically.

Let me explain the background: as you no doubt know, a great deal of work has been done developing computer systems for mathematics. Most of that work has been oriented toward developing rigorously (or near-rigorously) correct systems for reasoning, like Mathematica and Lean9.

My essay observes that in creative mathematical practice much of the most important work is far from rigorously correct. Instead, it's extremely heuristic, often relying on many analogies, pictures, and so on – things which are in some sense "wrong". The reason is that in the exploratory stages it's much more important to explore for ideas and understanding than to have detailed reasoning right. Getting the detailed reasoning right is often (not always) done later, and is often comparatively easy, given a powerful set of basic ideas.

And so I wondered whether there might be a kind of logic of heuristic discovery, that could be used to build computer interfaces to support heuristic exploration. The essay makes some technical progress toward this goal. But it's relatively minor: the essay is mostly about evoking the broader vision. I fondly imagine that if I'd written a half dozen technical followups, others might have come on board searching for logical foundations to support interfaces for heuristic exploration. Maybe they would have, maybe they wouldn't. But with the small amount of technical progress in my essay, it's understandable others didn't rush in.

It's interesting to contrast such a failed (or at least, not-yet-popular10) vision with Kay and Kitaev's papers. Both Kay and Kitaev made very strong technical progress (though with Kay the technical progress was mostly later). And that technical progress encouraged other people to explore those visions. It provided proof that such technical progress could be made, and gave people a stock of foundational results to explore and build off11.

Given all the above, it's not surprising pure vision papers often have a hard time getting published or taken seriously. Scientific communities (and journals) work hard to create strong standards for what counts as a scientific result that advances our understanding. Visions violate those standards, and so there are high barriers to being published or taken seriously.

The standard way of sneaking visions in is thus under the radar: it's to accompany them with strong technical results that make up the (supposed) meat of the paper. Sure, the vision stuff may seem wishy-washy and of dubious long-term importance, but a certain amount will be tolerated by editors and referees if it seems to be backdrop against which the hard-nosed, no-nonsense technical results are built.

Curiously, though, when such a vision is successful, even partially, the early technical results are often forgotten. Having used my own past work above as an example of failure, I hope you'll forgive me for mentioning a more successful example. It was developing a set of ideas about quantum computing as a type of high-dimensional geometry. The idea is to show that the path of an (optimal) quantum computation can be thought of as freely falling along the geodesics of some high-dimensional space. The local geometry of the space tells you how to optimally quantum compute.

I believe this is a beautiful vision. But I doubt it would ever have been published if my collaborators and I hadn't found a way of making the basic idea work, technically – a detailed construction of the geometry, proofs of the basic properties, and then quite a bit of technical progress in understanding the geometry12. We got a solid technical foothold, and pointed the way to further progress. That technical progress certainly helped us get published, and encouraged other people to get involved. Those people have since vastly improved many of the original technical ideas – much of the technical stuff we did has now been replaced by significantly better constructions. But those better constructions make the original vision look more compelling, not less, even while making many of the early technical results obsolete. Furthermore, the original vision has also been strengthened and changed in ways that greatly surprised me – for instance, there are now many people thinking about this kind of geometry as a way of understanding black holes13.

Who writes vision papers? A friend observed that they couldn't imagine most scientists they know writing a vision paper. That comports with my own impression. I don't think it's for any intrinsic reason – there are many scientists who are extremely imaginative and bold and insightful, but I'd be surprised if they wrote such a paper. Rather, I think it's because writing such papers requires a very different skillset than writing normal papers. I believe you likely need a substantial amount of conventional scientific insight to write a great vision paper; but you can be an amazing scientist and not have the skills (or interest) in writing such a paper.

That said, let's come back to the question asked earlier: to what extent is this a skillset worth actively cultivating? Is it a good idea to be publishing your own vision papers?

John Maynard Keynes famously said: "Practical men who believe themselves to be quite exempt from any intellectual influence, are usually the slaves of some defunct economist. Madmen in authority, who hear voices in the air, are distilling their frenzy from some academic scribbler of a few years back."

There's some truth to an analogous idea in science. If you don't develop your own vision, then you're likely to be working inside someone else's. There's nothing wrong with that – indeed, it can be immensely generative of good work. But if you desire a certain kind of intellectual autonomy then you'll want to set your own path.

I said you'll "likely" be working inside someone else's visions. In fact, it's only somewhat true. Visions often emerge post hoc out of specific, detailed problems, not overarching visions. Einstein didn't start out with some vision of changing our notions of space, time, mass, and energy. It's hard to trace his exact thinking, but it certainly started out a lot more detailed than that – most likely (though himself seems to have been somewhat unclear) trying to understand some seeming inconsistencies in Maxwell's equations. Similarly, Planck didn't start out with a vision of fundamentally reforming how we think about reality. He was just trying to understand how much energy there is in the electromagnetic field inside a cavity.

The relationship to science fiction: I occasionally meet non-scientists who think scientists lack a certain kind of willingness to dream big. I've heard it said that that they could stand to use a bit more of the science fictions writer's willingness to speculate.

This idea is plausible, but based on a false premise. In most science fictional scenarios, what is insightful (in the science) is not original; and what is original is not insightful. The reason is straightforward: to write a paper like Kay's or Kitaev's – or the other examples mentioned in the opening – requires tremendous foundational insight. It's that insight which enables the vision. Science fictional speculation is often flashy, and fun, and has good narrative hooks; but there's no particular need for foundational insight. Nature is more imaginative than we; when Kitaev figures out that it might be possible to build naturally fault-tolerant materials, that's an extraordinary insight into latent possibility in the natural world; it's not because he has a strong narrative imagination. The best vision papers come from people who have seen something never before glimpsed in Nature, and are reporting it back to the rest of us.

There are exceptions to this rule. Ideas like geosynchronous orbit, nuclear weapons, and the singularity are sometimes attributed to science fiction writers. This is often ahistorical: Arthur C. Clarke did not, for instance, invent the idea of geosynchronous satellites, as is sometimes mistakenly said. But he did popularize the idea, and write about it in an insightful and original manner. Of course: there's no a priori reason science fiction writers can't do this kind of work. But what science fiction selects for is narrative depth and plausibility, not insight into nature. The most important visions seem to be built on the latter, not the former.

With that said, science fiction writers often are genuinely good at reasoning about science and technology at a different level of abstraction than the way most scientists engage with it. The writer Steven Johnson coined the phrase "the long zoom" to describe the ability to zoom in and out over many levels of detail. Science fiction writers often operate better at certain levels of zoom than do many scientists. That's perhaps what's going on here: people good at writing vision papers are people who simultaneously have tremendous technical strength and insight at the scientist's usual level of detailed understanding, and simultaneously have a science-fictional like ability to think in the long zoom, and are willing to defy social convention enough to write about it.

What I'm not saying: One hesitation I had in writing these notes was over-venerating visions. I think this kind of work is undervalued in science, but it certainly wouldn't be appropriate to adopt norms from elsewhere. Silicon Valley is organized around (and venerates) a related kind of vision – that's how people pitch their companies to potential employees, investors, and companies. It's good as a way of co-ordinating action, but the qualities that make it useful in Silicon Valley have little correlation with a good scientific vision. For example, being brief and pointed is highly valued in company pitches, and it's easy to see why: there's value in being able to briefly explain to customers what you're doing for them. But nature has no such constraint, and many important scientific issues take hours (or more) to appreciate.

(This is a perpetual source of frustration in Silicon Valley dinner-party conversation. Them: "So, what do you research?" Me: "[attempts, unsuccessfully, to be both brief and legible]". Often, you can see the thought, occasionally explicitly voiced: "that doesn't sound very promising". But the person is using their startup-evaluation criteria to evaluate my research. If I use my research-evaluation criteria, their startup idea usually stinks, too. They have no useful model of how to think about research, boiling everything down either to: "Could I imagine this being used someday in a company?", or, if they're a bit more broad-minded: "Does this sound like research work I've previously heard is important?")

In science, it's not necessary to have a clear vision in advance. Many of our most celebrated discoveries were made largely without the help of such visions. Certainly, Newton, Darwin, and Einstein didn't begin with a clear vision. To the extent we attribute any such "vision", it is pasted on, after-the-fact. Newton didn't begin by trying to develop "the System of the World". Indeed, he spent a tremendous amount of time on rather arcane, even illegible technical problems. The system of the world is where he ended up. Similarly, we tell neat post hoc stories about Einstein as a precocious 16 year-old, wondering what it would be like to travel on a light beam. But the reality of Einstein-the-young-physicist that emerges from his biographies is far less legible, and much more focused on nuts-and-bolts technical problems. And as for Darwin: he thought his principle purpose on the Beagle was geology, with biology a sideline. He didn't even know what field he was working in. These aren't people pursuing vision; they're people doing instinctive exploration of subjects they feel to be deep, and solving technical problems; that work changed what we think of as scieence, but it wasn't emerging out of any vision.

Conclusions and questions

Alright, that's a brain dump of a few thousand words. Of course it barely scratches the surface. It's just scratching around, trying to get purchase on the problem. It may be that someone has previously investigated this in depth, maybe in the philosophy of science, STS, or adjacent communities. But if so, I'm not aware of it.

What have we learned?

Let me begin with the most directly personal question: should one feel sheepish about writing vision papers? Is it actually a worthwhile activity?

It's clear the answer is somewhat personality-dependent. But if it's an activity you find attractive, then it can be valuable, if cultivated and you hold yourself to high standards. The sense that it's a waste of time is a side effect of internalizing community prejudices against such papers. Those community prejudices are in place for sound reasons: the papers fall afoul of the usual standards for technical progress. There's tremdendous value in (usually) enforcing those standards – it keeps science from going off the rails, and journals from being places full of untramelled speculation, speculation which cannot be built off.

The trouble with vision papers is that those community standards dissolve. It's difficult to say clearly what distinguishes a good vision from a bad one, except ex post. But there can nonetheless be tremendous personal value. If you sense a latent possibility that is not common knowledge, then writing such a paper helps you improve your understanding of that possibility, why it may be important, how you might move toward it, and how it might fail14.

The physicist John Wheeler once stated a useful principle to guide research: "In any field, find the strangest thing and explore it."

Vision papers often have at least part of this "strangest thing" quality. If they identify genuinely new possibilities, then those things have the strangeness of novelty, of being possibilities just beyond what human beings have ever identified before. That said, the danger in indulging such work is that you're then operating (in many ways) outside conventional guardrails. It's easy to confuse being a misguided dreamer with being a bold iconoclast. Some common warning signs:

I meet a fair number of people of the latter type in Silicon Valley-adjacent people who disdain scientific work. They think of themselves as "bold idea" people. But it's hard to have good ideas when you're not intimately familiar with details. Those people often look down upon "incremental" work. But it's hard to think of someone with great vision who wasn't also exceptionally good at cranking out incremental papers.

A distinction I didn't discuss in the body of the notes is between organizational visions and scientific visions. Organizational visions are things like the human genome project, where the scientific object of interest (the human genome) was perfectly obvious to everyone for years or decades prior to the project. It was not a new scientific insight. Rather, the vision in such cases is mostly or entirely organizational. Scientific visions, by contrast, are different: it's some new possibility in nature which is being evoked – Kay's vision of new media for learning and thinking; Kitaev's vision of materials which naturally want to quantum compute.

Sometimes there are intermediate possibilities. LIGO required both an incredible set of scientific insights, and also a remarkable organizational vision.

My own personal interest is much more on the scientific vision side. I mention this because: (1) the skills involved in the two cases are very different; and (2) scientific visions are usually far less legible, making it more challenging – even for the originator – to evaluate the worth of what they're doing. The reason is because, as mentioned above, organizational visions are typically about scientific possibilities that have been known for many years. The uncertainties lie elsewhere.

Let me finish with a few questions:


For conversations on this subject, thanks to David Chapman, Laura Deming, Adam Marblestone, and Kanjun Qiu.


  1. These are not necessarily papers, but may be books, grant proposals, lectures, presentations, and so on. In these notes I use vision paper as a catchall phrase.↩︎

  2. A few vision papers I very much like: Gordon Moore's 1965 paper on his now-eponymous law; Doug Engelbart's 1962 paper on augmenting human intelligence; Rainer Weiss's early work on gravitational wave detection (and some followups, e.g., the 1983 NSF report on LIGO – many megaprojects presumably start out with visionary grant proposals); Lynn Margulis on endosymbiosis, and her collaboration with Lovelock on Gaia; the early papers on connectomics, circa the early 2000s; Alan Turing's 1950 paper on artificial intelligence and his 1952 paper on morphogenesis; David Deutsch's 1980s papers on quantum computing; Ted Nelson and Bret Victor's many wonderful imaginings about the future of media, thinking, and computers; Claude Shannon's 1940s papers on information theory; Neal Stephenson's book "The Diamond Age"; parts of Vernor Vinge's work; Tim Berners-Lee's proposal for the web; Adam Marblestone's proposals, many of which involve mapping or interfacing with the brain in some way, but which also branch out into other areas; Richard Feynman's papers on quantum computing and molecular nanotechnology; Freeman Dyson's multiple visions of future technology. Curiously, all but one of these people are men. In part this is because most of the papers have been around for quite some time, and science used to be more male-dominated. It's partly because I'm most familiar with physics and adjacent fields, which are also more male-dominated than most sciences. Still, I'd be curious to hear of more vision papers from women.↩︎

  3. This is another fuzzy, hard-to-prove assertion, in part because the category is, of course, quite vague.↩︎

  4. Kay wrote several later papers developing many of the ideas in the 1972 paper (sometimes with collaborators). I've read many of these papers multiple times, and it's now difficult for me to read the 1972 paper except in the light of those later papers. As I wrote these notes I realized that in my thinking I occasionally attribute to the 1972 paper ideas that are only hinted at there, and which only really appear in later work, often in somewhat different forms. I'm a little self-conscious about over-attributing importance to the 1972 paper. Still, I think there genuinely are hints of many of the most important later ideas there; in that sense, it is a vision, evoking something wortwhile and new, even if only very partially revealed.↩︎

  5. The phrase normal science was made famous in Kuhn's "Structure of Scientific Revolutions", by contrast with what Kuhn called revolutionary science. The "normal" versus "visionary" paper distinction is different, though. While there's a lot insightful in "Structure", Kuhn's division into "normal science" and "revolutionary science" is often misleading. I won't justify that opinion – it would require a long essay. I'm simply starting what I believe, and the consequence that there's no particular reason vision papers should be about Kuhn's revolutionary science.↩︎

  6. Albeit, not necessarily in exactly the direction laid out. For instance, many people say their work was inspired by "A Personal Computer for Children of All Ages". But much of that work is in somewhat (or even radically) different directions from the original vision. I believe this exploration in diverse, even contradictory, directions is (mostly) a feature, not a bug, though the original visionaries don't always agree!↩︎

  7. Writing this makes me realize I don't understand well the distinction between a technical result and a story, either.↩︎

  8. I'm still dissatisfied with this. Of course, people do build upon and modify visions all the time. But again it's much more concerned with the behaviour of scientists than with the behaviour of things in the world.↩︎

  9. With some caveats. I imagine many proponents of proof assistants are either aghast or amused by my characterization of Mathematics as supporting "rigorously correct" reasoning. You can certainly abuse Mathematica, getting it to engage in useful-but-not-rigorously-correct reasoning. And it wouldn't surprise me if the same is true of Lean, though it's perhaps harder. But in both cases the underlying design goal seems to be to use the system to support correct reasoning, not heuristic exploration.↩︎

  10. It's hard to tell the difference between failed visions, and those whose time hasn't yet come. Certainly, many vision papers languish for years or decades, before revival.↩︎

  11. As a practical matter, they're often the grist out of which careers can be made. I don't mean to be cynical: provided it doesn't become an overwhelming force, careerism can be a powerful force for the advancement of science.↩︎

  12. See, e.g., here and here, and references therein.↩︎

  13. An early paper in this vein is, for example, Susskind and Zhao (2014).↩︎

  14. That sounds a lot like a grant or a job application. In practice, there's a lot of distorting factors in those. I don't think I've ever read a grant application that seemed especially compelling as a vision, and I certainly don't think it's because the authors weren't (in some cases) capable. Rather, there's something strange about the constraints of the form. Vision statements in job applications are more variable – the best sometimes seem quite compelling.↩︎