I. Traversing the Landscape of Scientific Knowledge
Consider a landscape in which peaks represent scientific knowledge and valleys represent all that is false, irrational, or ill-conceived. Scientific progress depends on our ability, as individuals and as a scientific community, to (1) find new peaks and to (2) climb them. These two sub-goals require two fundamentally different modes of travel, what I will call wandering (i.e. random walk, or the explore in explore/exploit) and climbing (hill-climbing in algorithmic parlance). As will become clear momentarily, I have chosen these terms over the more conventional explore/exploit dichotomy because I have something in mind that is a little more expansive and multi-dimensional than is typically implied by that framing.
We begin by considering the wandering/climbing distinction at the level of an individual scientist and their research activities. Climbing is what Yanai and Lercher, and Francoise Jacob before them, call Day Science, “…the one you read about in the news, it is the one we learn about in school, the one captured by the phrase “hypothesis driven”. It’s epitomized by the women and men in white lab coats holding pipettes or looking intently at a computer screen. A day scientist is a hunter who has a clear picture of what she is pursuing.” Night science then is wandering, something that is made explicit in the following passage, “…it wanders blind. It hesitates, stumbles, recoils, sweats, wakes with a start. Doubting everything, it is forever trying to find itself, question itself, pull itself back together. Night science is a sort of workshop of the possible where what will become the building material of science is worked out”.
Nobel prize-winning biochemist Albert Szent-Györgi used different terminology to describe these same basic categories of scientific activity in a 1972 letter to Science.
In science the Apollonian tends to develop established lines to perfection, while the Dionysian rather relies on intuition and is more likely to open new, unexpected alleys for research…The future of mankind depends on the progress of science, and the progress of science depends on the support it can find. Support mostly takes the form of grants, and the present methods of distributing grants unduly favor the Apollonian. Applying for a grant begins with writing a project. The Apollonian clearly sees the future lines of his research and has no difficulty writing a clear project. Not so the Dionysian, who knows only the direction in which he wants to go out into the unknown; he has no idea what he is going to find there and how he is going to find it. Defining the unknown or writing down the subconscious is a contradiction in absurdum.
The ancient dichotomy of the Apollonian (order, logic, restraint, harmony) and the Dionysian (chaos, emotion, intuition, orgiastic revelry) provides the psychological bedrock upon which the higher-level dichotomy of climbing and wandering is built. This points us towards a crucial, perhaps the crucial, difference between our two modes of travel: climbing is about the quantifiable (the logic can be traced, the calculations can be checked, the data can be analyzed) while wandering is about the unquantifiable—ideas, intangible and ineffable, their value, causes, and consequences only knowable in hindsight, if at all (more on this later).
These two modes of individual scientific thought and activity also flow upward into contrasting epistemological orientations and organizational principles for the scientific community as a whole. To understand why this is so, let’s treat the climbing metaphor very literally by considering the first confirmed ascent of Mount Everest in 1953 by Edmund Hillary and Tenzing Norgay (George Mallory and Andrew Irvine might have reached the summit in 1924, but they died during the descent). The ascent was a massive operation, taking over 2 months from base to summit and requiring years of planning (great care was taken to select the most expert mountaineers), training (the principles of the crew trained in Wales before the ascent), and reconnaissance. The crew of over 200 climbers and porters was led by John Hunt, a British army colonel, and for all intents and purposes was a military operation.
From this brief description, we can draw several lessons about the nature of climbing that apply whether the mountains are made of rocks or knowledge. Mountain climbing is a collaborative activity that requires some degree of hierarchical, top-down command. The ascent of truly challenging mountains requires the financial and administrative support of a large centralized institution (for Everest, it was the British military; for “knowledge mountains”, it is universities and funding bodies like the NSF and NIH). Climbing also requires special skills than can only be developed through extensive training (often provided or supported by those same large centralized institutions); following from this, some kind of vetting or credentialing process is needed to determine who are the best mountaineers. Lastly, mountain climbing is an inherently dangerous activity (the first pair chosen for ascent to the summit had to turn around due to equipment failure—climbing also requires equipment) and therefore is generally conservative in nature. This is not to say that climbing can’t be a highly risky endeavor, but that there is a general defensive posture which must be taken while ascending any significant peak.
To recap: climbing is collaborative, hierarchical, top-down, centralized, institutionalized, and conservative. It requires significant amounts of money, equipment, and training and therefore is professionalized, standardized, and homogenized (you don’t want any equipment surprises halfway up the mountain and you need to trust that your fellow climbers aren’t going to deviate from the plan and put everyone in danger). All of these qualities of climbing are interconnected and in some sense implied by the very nature of the activity.
Climbing leads to a specific form of scientific progress that has been variously characterized as incremental, “normal” science (in the Kuhnian sense), or “standing on the shoulders of giants in order to see further”. Climbing is the mode of science that aims towards known targets and clearly defined goals. The Manhattan project is a quintessential example of climbing science as I have described it here, and as such it shouldn’t be surprising that it was ultimately a military operation just like the first ascent of Mount Everest.
Wandering is the antithesis of climbing, its equal and opposite. It is those scientific endeavors that are individualistic, decentralized, egalitarian, unsystematized, unstandardized, and bottom-up. Wandering is revolutionary, paradigm-shifting science, the kind of science that finds entire mountain ranges of knowledge that were heretofore unimaginable (the unknown unknowns).
This metaphor has already gotten a little too unwieldy (a little?), but let’s add another metaphor into the mix in hopes that this will simplify our understanding of the first: climbing is religion and wandering is spirituality (much more on this in the final section).
II. Climbing and its Discontents
I hope that one thing is obvious at this stage—neither climbing nor wandering is inherently better or more useful than the other, and both are equally necessary for robust scientific progress. The challenge is to find the optimal balance between the two, a task that is complicated by the fact that the optimal balance is itself a moving target (e.g. physics may require more climbing than psychology at their current levels of advancement. What would be the equivalent of the Large Hadron Collider for psychology? We have no idea.). For most of scientific history, we suffered from a lack of climbing capacity—the scientific community was too distributed and unorganized, and there was not an enough emphasis on brick-by-brick experimentation and data collection. Now, I think it is fair to wonder if the pendulum has swung too far in the other direction, if what modern science suffers from is an excess of climbing.
I believe there are a few broad historical trends that in combination have served to tilt science too far towards the climbing end of the spectrum. To some degree, all of these trends are the result of scientific progress, and in this sense science has simply become a victim of its own success. This is seen perhaps most clearly in the inevitable consequences of knowledge accumulation, the so-called “burden of knowledge”. As knowledge grows, successive generations of scientists face a greater educational burden (i.e. there is more to learn in order to reach the frontier of a field). This growing burden necessitates longer educational periods and/or narrowing expertise, both of which reduce the capacities of individual thinkers. These compensatory moves compel a shift towards educational schemes/institutions which favor efficiency and standardization (i.e. there is a lot to learn so we need to learn it quickly and figure who knows it and who doesn’t) and towards a greater reliance on team science.
All of this is to say that we should naturally expect a shift towards climbing (team-oriented, institutionalized, efficient, standardized, professionalized, etc.) as a consequence of growing scientific knowledge. To put this point in metaphorical terms: when the “shoulders of giants” are low, it is conceivable that one individual can scale the shoulders by themselves, but teamwork and efficient standardized training are required when the giants truly become gigantic.
So the burden of knowledge creates a significant pressure towards climbing science, however on its own this pressure should not be enough to swing the pendulum too far in this direction; in fact, if the burden of knowledge were the only factor influencing the climbing/wandering balance then we would likely expect it to track optimally with the current state of scientific knowledge. We should look then for forces that have enhanced the underlying trend towards climbing beyond what is inevitable with a growing burden of knowledge.
Tyler Cowen has argued that the development of modern transportation, communication, and industrial technologies over historical timescales has enabled the bureaucracy needed to sustain the large powerful governments and corporations that we see today. Though Cowen doesn’t discuss this effect in the context of scientific organization, there is no reason to think that these same technological forces wouldn’t be acting here as well.
Interestingly, Cowen describes the phenomenon of “governmental overshooting”.
“…it appears that new technologies enabled the spread of a fascist intoxication with power, both among leaders and the general citizenry…Political and cultural institutions were not well equipped to handle the social implications of the new technologies of radio, electricity, and easy transportation. Those technologies made mass culture possible and in the realm of politics that mass culture translated into fascism. Only after bitter experience did fascist ideas become less popular and social and political norms subsequently evolved to protect electorates against the fascist temptation.”
This provides a good model for the notion that science has overshot the optimal balance between climbing and wandering. We could argue in the same manner that this technological climate enabled a kind of “intoxication” with centralized institutional power in science (culminating in the Manhattan project and the space race) that we have not yet learned to pushed back on by evolving new norms and values.
Dovetailing with this trend towards increasing centralization is the steadily growing importance of science and technology to national security; the confluence of these two forces has resulted in our current situation in which the entanglement of science and government is at all-time high. The corrupting influence of politics on science is well documented, but there is another more subtle issue that arises as the scientific community becomes intertwined with the governmental apparatus. In Seeing like a State, historian James Scott discusses how governments have sought over time to increase the legibility of their populace by imposing policies that make it easier quantify and keep track of people and property (e.g. social security numbers, the collecting of census data, the gridification of cities, standardized measurements, uniform languages, etc.). I think we can argue that a similar thing has happened as governments have increasingly become sponsors and organizers of science—there has been a mass shift towards greater legibility of all the inputs (money, equipment, administrative support) and outputs of research (publications, citations, patents, awards, etc.). Computers and the internet have been rocket fuel for legibility, easily allowing us to track nearly every aspect of the scientific enterprise.
I would argue that this intense “metrification” is responsible, either directly or indirectly, for much of what’s wrong with science. Much ink has been spilled on the nature of these issues so I won’t belabor the discussion, but suffice it to say that many of the metrics used to evaluate scientists and their research serve to incentivize conservatism and easily-quantified productivity over risk-taking and the development of new ideas (which, as previously noted, are by their very nature unquantifiable) (See Matt Clancy’s “Conservatism in Science”). In essence we have created a system where scientists are disincentivized from doing anything that won’t help them publish more research or bring in more grant money—performing replications, sharing data or ideas, mentoring undergraduates, improving their teaching, etc.
Some of these problems with metrics are due to the unsophisticated use of simple metrics and it should be possible to alleviate these problems with better metrics and greater awareness of their strengths and weaknesses. That being said, there are also some more fundamental issues that arise from the very nature of metrics and the incentive structures they create. It is easy to say that we need more complex metrics, but greater complexity comes with its own costs (e.g. more data might be needed to develop the new metric, more bureaucracy needed to collect that data, less intuitive metrics are less likely to be understood and correctly applied). Metrics, whether complex or simple, always suffer from the curse of Goodhart’s Law – “when a measure becomes a target, it ceases to be a good measure” (see the Eponymous Laws series). For example, citation counts may have been a good proxy for a scientist’s influence when we first started using them, but now that scientists are aware of their importance they have become a less effective measure because scientists are incentivized to game the citation counts however they can (publishing in hot research areas, rushing flashy results to publication without careful replication, developing superfluous new terms or metrics in hopes that they will catch on, self-citing). We might also mention here that citation norms themselves represent an implicit epistemological orientation that predisposes one towards incremental research that clearly builds off previous work (i.e. climbing) at the expense of truly novel ideas that might not have clear antecedents (I could provide a citation for this point, but I refuse to do so as an act of civil disobedience). Lastly, it is fair to wonder about the psychological cost of excessive metrification. I’m no expert here, but the awareness that your work is constantly being measured on a variety of dimensions probably isn’t conducive to creativity, job satisfaction, or mental health.
It might be helpful to make explicit something that has been lurking in the background of this section: the role of the internet in the scientific enterprise. The internet is, I think, usually seen as an unequivocal boon for science as it allows greater access to information and rapid communication between scientists (amongst many other benefits). My contrarianism runs deep, but not quite deep enough to deny that the internet has been, on balance, a good thing for science. But there is a balance, and I don’t think we have fully grappled with the costs of this mass shift in scientific thinking and doing. To put it in the terminology of this essay: the internet has supercharged our ability to climb but subtly (or not so subtly) harmed our ability to wander. In his song “Welcome to the Internet”, comedian-troubadour Bo Burnham sings, “Could I interest you in everything all of the time?”; I’m not the first to say it nor the last, but there is something incredibly unnatural about this everything-all-the-time state of affairs and it seems more than likely that it is warping our creativity and cultural dynamics in a problematic manner. Derek Thompson speculates on this theme in his recent article “American is Running on Fumes”:
The world is one big panopticon, and we don’t fully understand the implications of building a planetary marketplace of attention in which everything we do has an audience. Our work, our opinions, our milestones, and our subtle preferences are routinely submitted for public approval online. Maybe this makes culture more imitative. If you want to produce popular things, and you can easily tell from the internet what’s already popular, you’re simply more likely to produce more of that thing. This mimetic pressure is part of human nature. But perhaps the internet supercharges this trait and, in the process, makes people more hesitant about sharing ideas that aren’t already demonstrably pre-approved, which reduces novelty across many domains.
Lest I be mistaken, I am not advocating for the abandonment of metrics and centralized science (or the internet, as if that were even possible or desirable). This would amount to a return to the scientific anarchy of the pre-modern era, i.e. a science that is all wandering and no climbing. The challenge then, as I see it, is to find a way forward that allows us to overcome the bad incentives and constraints that make it difficult for scientists to freely wander while also maintaining the benefits of big institutional science.
III. Not All Who Wander are Lost
In his essay “We Don’t Know How to Fix Science”, José Luis Ricón argues that while we have many good ideas about how to reform science we need more meta-scientific experimentation to determine if these reforms will actually work. While I am certainly on board with more meta-scientific experimentation, I am dubious that this will “fix” science or even really improve it in any kind of significant way. Ricón is realistic about the difficulties of evaluating these kinds of experiments—the results may only become clear over the long term, a policy that has positive effects in a small experiment (e.g. shifting the length of a grant) might not scale—but remains optimistic that they will help us learn how to slowly improve science policy. My skepticism towards this whole philosophy comes in part from a striking passage in the essay:
Statistician Adrian Barnett reports having talked to Australian funding agencies asking them about using a lottery to allocate their funding. The reply didn’t involve, as one might have expected, a lack of belief in the effectiveness of lotteries. Rather, the answer he got was that “It would make it look like we [the agency] don’t know what we’re doing.”
Such is the nature of institutions—they will act to preserve the problem for which they are the solution (the Shirky principle). Producing evidence for new policies is one thing; implementation is another. The scientific ecosystem is so complex, and the interests so entrenched, that I am pessimistic about our ability to effect real top-down change. Moreover, I worry that even when we do effect structural change often times all we really accomplish is a shift to a new equilibrium that has different constraints and different bad incentives (goodharting never stops). Alexey Guzey hits the nail on the head in his recent essay “New Incentives will not Save Science”.
So then what will save science?
You. You are going to save science.
Musing on Marc Andreessen’s widely circulated 2021 essay “It’s Time to Build”, Tanner Greer quips that, “In the 21st century, the main question in American social life is not “how do we make that happen?” but “how do we get management to take our side?” (“On Cultures that Build”).
Management will never take our side. Fuck management.
Do not try to change governmental institutions, universities, scientific journals, or the “scientific community”. Everyone is busy, no one wants more work to do, and no one gives a shit about what you have to say. There is no grand top-down scheme that will magically alleviate all of the problems in science. There is no quick fix and there never will be.
As I have argued, our current scientific epoch is characterized by an overabundance of this multi-dimensional constellation of qualities that I have termed climbing—goal-oriented, collaborative, institutionalized, centralized, professionalized, hierarchical, legible. The only way to remedy this excess is to lean radically in the opposite direction, that is to wander, and to do so fiercely. More than anything, this means an utter and complete rejection of anything that doesn’t start with the individual. The revolution will not trickle down from the top; it will bubble up from the bottom, from deep within the minds and hearts of each and every one of us. All of this obsession with meta-science and institutional design is just a cop-out. It’s easy—do an experiment, change a policy, build an institution, and voila!—no more publish or perish, no more endless grant writing, no more bad incentives, science enters a new golden age and we all live happily ever after.
There is no way around it: you must look in the mirror and ask yourself, moment-by-moment and day-by-day, if you are truly embodying the deepest values of science— creativity, courage, openness, honesty, tolerance, humility, collegiality, and the rest. As if this wasn’t hard enough on its own, there is an enemy in this endeavor that conspires to thwart us at every turn, what is variously known as The System, The Man, The Machine, or Moloch.
The System desires to suppress all which cannot be measured, classified, controlled, manufactured, or predicted. It wants to sap you of your creativity, drain you of your joy, and turn you to cynicism (if you have found yourself thinking that all of this is idealistic bullshit then you are already lost). Those things which cannot be measured—ideas, inspiration, wonder, beauty, faith, hope, love—are grave threats to the System because they are, by their very nature, irrational, unpredictable, uncontrollable.
The Machine wants conformity, efficiency, and productivity above all else. It wants you to bend the knee, to sell your soul, to sacrifice all that you hold dear in the name of faster and faster and more and more. It wants you to forget that bad incentives can and should be resisted, that rules are meant to be broken, that at all times you have the right to say fuck this shit, I’m out.
“And this I believe: that the free, exploring mind of the individual human is the most valuable thing in the world. And this I would fight for: the freedom of the mind to take any direction it wishes, undirected. And this I must fight against: any idea, religion, or government which limits or destroys the individual. This is what I am and what I am about.” – John Steinbeck
The System wants you to think that scientific progress only comes from “the hard slog of large armies of individuals, each making—at best—a tiny step or two forward”. It whispers in your ear, “To think that you could be the next Darwin, the next Einstein, the next Newton—what arrogance! Please be realistic, think about your career! Just keep your nose to the grindstone and maybe one day you’ll be a real scientist, with a fancy PhD, a lab coat, and a published paper to your name.” The System wants you to think that all of the mountains of scientific knowledge have already been discovered (all that is left are known unknowns) and the only remaining task is to slowly schlep our way to the top.
I have to get you to drop modesty and say to yourself, “Yes, I would like to do first-class work.” Our society frowns on people who set out to do really good work. You're not supposed to; luck is supposed to descend on you and you do great things by chance. Well, that's a kind of dumb thing to say. I say, why shouldn't you set out to do something significant. You don't have to tell other people, but shouldn't you say to yourself, “Yes, I would like to do something significant.”
— Richard Hamming, “You and Your Research”
So I say unto you: wander fiercely, discover the Dionysian, pursue the paradoxical, embrace the irrational, welcome the wasteful, analyze the absurd, nurture inefficiency, find belief that cannot be shaken, and cherish all that cannot be measured.
These are your marching orders, but let’s talk boot-on-the-ground tactics.
- Productivity is the death of creativity. Do not listen to the voice in your head that chides you for reading fiction, for taking naps, for taking long walks.
- Institute a practice of “Great Thoughts Friday”— only grand speculative thoughts are allowed after lunch. Similarly, Steven Byrne encourages you to adopt “Solve the Whole Problem Day”—set aside a day in which you zoom out as far as you can and only consider your problem at the highest possible level.
- Most wandering leads to nowhere of interest. Do not expect an immediate payoff. Patience is a virtue. Creative hot streaks come only after long periods of exploration. Atypical papers featuring unusual combinations of prior work are nearly two times more likely to disrupt science than conventional papers, but this is a slow process taking ten years or longer (so-called “sleeping beauties”). Have faith that you are on the right path even if you don’t know where you are going.
- Give away your ideas. Do it early and do it often. But what if someone steals my idea? Let them. Your reputation for creativity and generosity will precede you. Others will come to you for discussion and share their biggest and wildest ideas. Whatever ideas you have lost will come back tenfold. Again, have faith.
- Another nugget of wisdom from Richard Hamming: work with the door open. From the previously quoted “You and Your Research”: “I notice that if you have the door to your office closed, you get more work done today and tomorrow, and you are more productive than most. But 10 years later somehow you don't know quite know what problems are worth working on; all the hard work you do is sort of tangential in importance. He who works with the door open gets all kinds of interruptions, but he also occasionally gets clues as to what the world is and what might be important. Now I cannot prove the cause and effect sequence because you might say, “The closed door is symbolic of a closed mind.” I don't know. But I can say there is a pretty good correlation between those who work with the doors open and those who ultimately do important things, although people who work with doors closed often work harder. Somehow they seem to work on slightly the wrong thing—not much, but enough that they miss fame.”
- Cultivate randomness. Engineer serendipity. The System hates randomness because it is unpredictable, and just in case my stance wasn’t crystal clear already—Fuck the System.
- Take drugs. Get higher than the shoulders of giants. Yes, this is completely irresponsible advice—that’s the point. The System wants you to be responsible. Say it two times—Fuck the System.
- Pay attention to your dreams. Keep a dream journal. Why? Because most scientifically-minded people don’t pay attention to them and it will make you different. Because dreams are randomized recombinations of your waking experience designed to prevent overfitting so paying greater attention to them amounts to turning up your mind’s randomness dial. Because dreams have played a role in previous scientific breakthroughs (Kekulé, Bohr, Mendeleev) and they will play a role in yours as well.
- Seek out underexplored or unexplored regions of the landscape of scientific knowledge. Where are people scared to go? What can’t people say? What is taboo? Go there.
Previously, I summarized the climbing/wandering distinction by saying that climbing is religion and wandering is spirituality. I know these are dirty words for most science folk, but I can’t think of a better way to characterize my argument. Religion is institutions and (rigid) hierarchy, honorifics and rituals, obedience and external displays of piety. Religion can be faked—are you really a holy man or do you just play one on TV? In contrast, spirituality pertains only to the individual and their personal quest for meaning and purpose, their personal struggle for virtue and transcendence. Religion is data and results—external and concrete, easily exaggerated or fabricated—whereas spirituality is ideas, intangible and immeasurable (you cannot fake a good idea or control it, at least not for long). This entire essay can thus be summarized as follows: science needs less religion and more spirituality.
It has been argued (by Niall Ferguson, Balaji Srinavasan, and no doubt many others) that the closest historical analogue of personal computing is the printing press, and that when trying to understand our current era we should look to the reformation instead of any intervening period. The reason our current era may be most similar to the reformation is that both the printing press and personal computing (along with the internet) were/are powerful forces for decentralization. In both cases, this is a significant reversal from the preceding era in which the technological climate (radio, TV, telephone) favored centralization and hierarchy (as discussed above). This should really worry us, Ferguson argues, because the reformation led to 130 years of escalating religious conflict, culminating in the Thirty Years War, one of the most destructive conflicts ever.
These same tensions are now playing out in the scientific domain. The pendulum has now swung towards decentralization and egalitarianism and those that would oppose these forces (academia, governmental institutions, corporations) are struggling to maintain their grasp on scientific power. Martin Luther launched a revolution that shook the world when he nailed his 95 theses to the door of All Saints’ church in Wittenberg; in these theses, he criticized the Church’s practice of selling indulgences and outlined a new spiritual philosophy that valued the primacy of the individual’s connection with God and rejected the Church as the only source of divine knowledge (he believed that if everyone could read the Bible it would create a “priesthood of all believers”). The internet has functioned as the door of All Saints’ Church; just as the church sold its soul for the indulgence money, we can now all see that science has also sold its soul (for grant money). Similarly, we need to develop a form of scientific spirituality, one that values the primacy of the individual and his connection, not with god, but with the core values and virtues of science (and yes I know that this means I am essentially comparing myself to Martin Luther which is just about the most grandiose and narcissistic thing ever, but so be it).
How can we develop this “scientific spirituality” and engrain it in the next generation of scientists? How can we launch the scientific reformation? I can imagine three paths forward. I’ve referenced Richard Hamming’s classic 1986 colloquium at Bell Labs “You and Your Research” a few times already, but let’s go back to the well one more time. At the end of the talk, there is a very interesting exchange during the Q&A session:
Question: The remarks about having courage, no one could argue with; but those of us who have gray hairs or who are well established don't have to worry too much. But what I sense among the young people these days is a real concern over the risk taking in a highly competitive environment. Do you have any words of wisdom on this?
Hamming: I'll quote Ed David more. Ed David was concerned about the general loss of nerve in our society. It does seem to me that we've gone through various periods. Coming out of the war, coming out of Los Alamos where we built the bomb, coming out of building the radars and so on, there came into the mathematics department, and the research area, a group of people with a lot of guts. They've just seen things done; they've just won a war which was fantastic. We had reasons for having courage and therefore we did a great deal. I can't arrange that situation to do it again. I cannot blame the present generation for not having it, but I agree with what you say; I just cannot attach blame to it. It doesn't seem to me they have the desire for greatness; they lack the courage to do it. But we had, because we were in a favorable circumstance to have it; we just came through a tremendously successful war. In the war we were looking very, very bad for a long while; it was a very desperate struggle as you well know. And our success, I think, gave us courage and self confidence; that's why you see, beginning in the late forties through the fifties, a tremendous productivity at the labs which was stimulated from the earlier times.
Perhaps WWIII will instill in us a new courage, a new sense of purpose that galvanizes the development of this spiritual ethos for scientists.
Peter Thiel has attributed the present state of scientific and technological stagnation to a lack of belief in secrets (i.e. the unknown unknowns). From Scott Alexander’s review of Thiel’s book Zero to One:
Past scientific discoveries came from a belief in secrets. Isaac Newton wondered why apples fell, thought “Maybe if I work really hard on this problem, I can discover something nobody has ever learned before”, and then set out to do it. Modern people aren’t just less likely to think this way. They’re actively discouraged from it by a culture which mocks stories like Newton’s as “the myth of the lone genius”. Nowadays people get told that if they think they’ve figured out something about gravity, they’re probably a crackpot. Instead, they should wait for very large government-funded programs full of well-credentialed people to make incremental advances.
As hinted at in that last sentence, Thiel attributes this lack of belief in secrets in part to incrementalism. From Zero to One:
From an early age, we are taught that the right way to do things is to proceed one very small step at a time, day by day, grade by grade. If you overachieve and end up learning something that’s not on the test, you won’t receive credit for it. But in exchange for doing exactly what’s asked of you (and for doing it just a bit better than your peers), you’ll get an A. This process extends all the way up through the tenure track, which is why academics usually chase large numbers of trivial publications instead of new frontiers.
To put this in my own terminology: too much climbing and not enough wandering. Thiel also points to the lack of a frontier as a culprit.
There are no blank spaces left on the map anymore…Today, explorers are found mostly in history books and children’s tales. Parents don’t expect their kids to become explorers any more than they expect them to become pirates or sultans. Perhaps there are a few dozen uncontacted tribes somewhere deep in the Amazon, and we know there remains one last earthly frontier in the depths of the oceans. But the unknown seems less accessible than ever.
This offers another source of hope as we finally seem on the cusp of opening the Martian frontier; perhaps the colonization of Mars will create a new zeal and sense of purpose for science. The development of a new scientific community on Mars will also offer a unique opportunity to start from scratch and rewrite the values, norms, and fundamental organization of science.
So we can imagine two developments that will spur us towards a scientific reformation: WWIII and the colonization of Mars. One of these options is not preferable for obvious reasons, but both of them have the disadvantage of being transient—the memory of WWIII will eventually fade and the martian frontier will eventually close. The third path forward is the most difficult, but it does have the potential to bring about a more lasting change. It all begins with a simple prescription, one that all of us can act on in this very moment.
“I maintain that truth is a pathless land, and you cannot approach it by any path whatsoever, by any religion, by any sect. That is my point of view, and I adhere to that absolutely and unconditionally. Truth, being limitless, unconditioned, unapproachable by any path whatsoever, cannot be organized; nor should any organization be formed to lead or to coerce people along any particular path.
(Originally posted at Secretum Secretorum)
There is a way to give away your idea in exchange for reputation: it's called publishing. You are even allowed (in the US at least) to patent same said (technical) idea for up to a year after initial publication. But if you freely give that idea to some interested party who can actually extract value, without first going through this acceptable route of publishing & publicizing, you're just giving it away for nil. I speak from experience.
Sure, I don't deny that there are some ideas which should be kept secret for at least some time so that you can better capitalize on them. But I think for most people this category of ideas is much smaller than they think and that it would serve them better in the long run to be less stingy with their ideas. This kind of gets to the crux of my thesis - if you have a scarcity mindset with ideas than they probably will be scarce for you. Maybe you will end up losing out on an opportunity or some concrete short-term benefit, but there are more intangible, long-term benefits to be had by being open with your ideas - the difficulty is that these benefits are inherently more nebulous/illegible and therefore easier to discount.