Far too many debates in the foundations of physics have this flavor. People mix up the vocabulary (primitives), the grammar (constraints), the dialect (formulation), and the meaning (interpretation).

Keeping these four levels separate makes it obvious that a lot of arguments are really just category errors. What's left are the questions worth spending time on.

Constraints and Primitives

When we want to describe nature we need to clarify what primitives and what fundamental constraints we are going to use.

One fundamental constraint, for example, is whether or not there is an upper speed limit. This is commonly encoded by the speed of light c being non-zero or infinity.

Another possible fundamental constraint is whether or not there is a fundamental minimum action (in the technical sense of the Lagrangian formalism).1 This is encoded by the Planck constant h being non-zero or zero.2

A third fundamental constraint is whether or not there is a minimum realizable energy density for empty space. This is encoded by the value of the cosmological constant Λ.

A useful way to understand many constraints is using the language of symmetry. A symmetry tells us what remains unchanged under what set of transformations. The speed of light constraint implies the correct spacetime symmetry group is not the Galilei group but the Poincaré group. The non-zero observed cosmological constant Λ implies that the correct kinematical group is the de Sitter group.

Similarly, we now know that fundamental interactions are governed by “internal” symmetry groups that we call U(1), SU(2), and SU(3).

On the other hand, the most common primitives are:3

1. Particles, which are localized at a single point

2. Fields, which aren’t localized at all, meaning instead of at a single point they are everywhere.

Note that we only decide here what the fundamental ingredients are, not what’s allowed to exist. Particles can emerge as excitations of fields. Fields can emerge as effective structures from particles if we zoom out.

Now, if we take particles as primitives, we end up with the following frameworks:4

If, on the other hand we consider fields as primitives, we get:

You can also have frameworks where both, fields and point particles, are fundamental like in Maxwell’s theory of electromagnetism.

This is all straightforward, and there is nothing controversial about this. We know from experiments that there is an upper speed limit and a minimum limit of the action. Hence, relativistic quantum theories are our best frameworks to describe nature at fundamental scales.

The other frameworks, on the other hand, can still be tremendously useful in cases where we can safely ignore these constraints. For example, when all the velocities are far below the speed of light, the upper speed limit has no meaningful impact, and we can use a non-relativistic framework.

Formulations

Where things do get a bit more tricky is when it comes to the choice of mathematical arena.

It turns out that you can describe each framework in a multitude of different mathematical arenas. Well-established arenas include Hilbert space, phase space, configuration space, or real space.

For example, the Hilbert space formulation of Classical Particle Theory is known as Koopman-von Neumann Mechanics while the configuration space formulation is known as Lagrangian Mechanics. The phase space formulation is Hamiltonian Mechanics. On the quantum side, we call, for example, the configuration space formulation Path Integral Formulation.

Each formulation is mathematically equivalent within a given framework. They make identical predictions for all physical observables. The choice between them is therefore not a matter of which is “correct” but rather which is most convenient or insightful for a particular problem.

For instance, Hamiltonian mechanics makes conservation laws transparent through Noether’s theorem, while Lagrangian mechanics often simplifies problems with constraints.

Looked at from this perspective, Bohmian mechanics is simply the real space formulation of non-relativistic quantum particle theory. Just as you can write classical mechanics in phase space (Hamiltonian) or configuration space (Lagrangian) or real space (Newtonian), you can write quantum particle theory in Hilbert space (standard textbook quantum mechanics) or real space (Bohmian mechanics).

Yet people routinely make a category error here. They treat Bohmian mechanics as if it were a competing theory rather than an alternative formulation. Then they argue that Bohmian mechanics is “disproven” or “fails” because no relativistic quantum field theory version has been successfully developed. But this gets things backwards. The lack of a fully worked-out relativistic field theory extension is not evidence against Bohmian mechanics as a formulation. It simply means the mathematical work hasn’t been completed yet.

Now importantly, I’m not claiming that Bohmian mechanics is superior as some Bohmian enthusiasts do. It’s simply a different formulation. Every formulation has trade-offs.

Consider an analogy: nobody bothers to work out Koopman-von Neumann mechanics (the Hilbert space formulation of classical particle theory) for complicated systems. Why would you? The phase space and configuration space formulations are far more useful for most practical purposes. But the absence of detailed Koopman-von Neumann treatments for most systems doesn’t mean the formulation “fails.” It just means nobody has bothered.

You can certainly argue about practical benefits of different formulations but this is an entirely separate discussion from questions about physical truth. The Hamiltonian formulation isn’t “more true” than the Lagrangian formulation or the Newtonian formulation.

Interpretations

Most discussions about interpretations similarly miss the point like discussions about formulations.

For example, the wave function is a mathematical object that appears in the Hilbert space formulation. It doesn’t appear in the path integral formulation. It doesn’t appear in Bohmian mechanics. Asking whether the wave function is “real” is like asking whether Hamiltonians are “real”. It’s treating a formulation-specific tool as if it were a fundamental feature of nature.

There’s little to learn from arguing about the reality of mathematical tools that only appear in certain formulations.

At the same time, I’m certainly not against having discussions on interpretive issues in physics. Just not these kinds of discussions.

Discussions Worth Having

What I like about the meta-framework outlined above is that makes it clear what areas are rarely explored and underdiscussed. It’s a useful lens to find questions worth asking.

Meaning of the Constraints

The fundamental constraints govern everything downstream. So if there are interpretative questions worth discussing it’s:

• What do these fundamental constraints mean?

• Where do these fundamental constraints come from?

The answer to the first question in the case of the speed of light limit might seem obvious but that doesn’t make it any less mysterious. How does it show up in different formulations? Are there any alternative interpretations that cast a different light on it?

Especially when we start adding quantum dynamics into the mix, questions of, for example,“locality” start to become a lot less obvious. Expressing the non-zero Planck constant constraint in terms of a minimal action or minimal phase space resolution does help but it’s far from what I would call satisfying interpretation. The same goes for interpreting the cosmological constant in terms of minimum realizable energy density for empty space.

Phase space is pixelated like a blurry jpg. Spacetime causality is bandwidth-limited. The universe has a lowest-frequency mode (or non-zero “idling” energy). But why?

Just as mysterious are the constraints that we are currently only able to articulate in terms of “internal symmetries”. Why exactly does the U(1), SU(2), SU(3) “gauge argument” work so spectacularly well in describing fundamental interactions?

Developing any ideas where these constraints come from would mean a huge step forward.

To give just a few quick ideas what this might look like:

• If we assume spacetime is discrete and no jumping on our spacetime grid is allowed, we automatically get an upper speed limit. That is no proof that spacetime is discrete, of course. But it’s an interesting, alternative perspective on how a constraint like this might arise.

• In the QBism interpretation of quantum mechanics, the non-zero Planck constant is understood as a “kind of coupling constant between subject and object” and hence quantum and classical theories “differ only in how they treat the subject-object relation”.

• In a “computational” interpretation, the cosmological constant Λ is the Garbage Collection boundary. While the speed of light (c) limits the latency of a single calculation and the Planck constant (h) defines the bit-depth of the data, Λ defines the Total Addressable Memory (RAM). By accelerating the expansion of space, the universe creates a “Cosmological Horizon” that effectively deletes distant, unreachable data from an observer’s local “cache.” Λ is the mechanism that ensures the simulation remains locally finite, preventing the system from choking on the infinite data of an infinite, static universe.

• Internal symmetries can be understood as remnants of bigger symmetries that spontaneously broke when the universe cooled down. This is a popular idea known as Grand Unification. However, it of course only pushes the real puzzle further down the line. Where do these “internal symmetries” come from and why exactly these symmetries instead of the infinitely many others possible? One approach is to derive internal symmetries from the structure of spacetime as in the Kaluza-Klein theory. However if the way this happens isn’t forced on us by the theory but something we put in, I’m not sure how much we are actually learning here. (Meaning if there are ways to get basically any possible group out of the process in principle and we are putting in a specific “compactification” scheme to get just the groups we need.)

Different Constraints and Primitives

In a recent essay I’ve outlined the “Games Mathematicians Play”: classifying all the things that can be classified and thinking through all the ways assumptions can be dropped.

In other words, a fruitful approach is often to explore all the different universes we can find a consistent description for. Even if there is currently no experimental evidence that we inhabit such an alternative universe, that doesn’t mean we aren’t living in one. The Planck, cosmological, and speed of light constraints, just like the shape of our planet or its place in the solar system, are far from obvious until you know where to look.

In our framework here this would mean asking questions like:

• What constraints that are on the same fundamental level as the speed of light, the Planck constant, and the cosmological constant could theoretically be added? So far, physicists only added these constraints when they were forced on us by experiments. But maybe there is a chance to get ahead of experimental discovery by exploring other possible constraints systematically.5

• What other primitives can we use? There is a whole spectrum of primitives that live somewhere between the two extremal cases of point particles and fields. The best known example is strings that are localized on a line instead of a single point. What if we use them without the ambitious idea to use them to unify everything and get rid of point particles?

• What modifications of spacetime are possible? What if it is discrete vs. continuous, curved instead of flat, a dynamic actor instead of a passive background structure, and what is its dimensionality? A lot of research has, of course, already been done on these questions but typically only within specific frameworks that come with a lot of extra baggage. Another lesser-known example: What if our usual abstraction using real numbers to label space and time is too idealistic? What would be the alternatives? (After all, if you take this abstraction seriously, you quickly run into paradoxes.)6

Dualities and Emergent Primitives

What if some primitives are not actually fundamental but emergent? How far can we push this idea?

In fact, a popular view is that fields are fundamental and particles only emerge as field excitations. If you want to be dramatic, you could say, “there are no particles, there are only fields”. Now fields are undeniably extremely powerful bookkeeping devices in situations where we are dealing with particle creation and annihilation like for example collider experiments. But then again, usefulness doesn’t mean it’s true.

So what about the exact opposite idea that particles are fundamental and fields are emergent structures?

Even more radical is the idea that we drop spacetime as a primitive. Can we build a consistent framework where spacetime with all experimentally known features emerges purely through the relations of the other primitives?7

And what about the opposite idea here? What if there is only spacetime and no other primitives? Particles or fields would need to arise purely from geometric features of spacetime. There is, of course, a good example of this already: General Relativity is able to explain gravity through spacetime curvature. Theodor Kaluza showed a hundred years ago that by extending spacetime to five dimensions, one could produce the Einstein equations in four dimensions, plus an extra set of equations that is equivalent to Maxwell’s equations for electromagnetism. Albert Einstein spent decades trying to make ideas like this work.

There are also ideas for how to understand internal symmetries as emergent.

Different Arenas and Formulations

Last but not least, the history of science shows that alternative formulations have tremendous value in casting fresh light on old problems.

So, what other formulations of our theories are possible? What other mathematical arenas are worth using?

We know that besides real and complex numbers there are only two additional consistent number systems: quaternions and octonions. So what about formulations in quaternionic or octonionic Hilbert spaces?8

Another interesting alternative mathematical arena to explore is Twistor space.

There’s no reason to think we’ve exhausted the possibilities. Hamiltonian mechanics wasn’t developed until fifty years after Lagrangian mechanics. The path integral formulation of quantum mechanics came decades after the Hilbert space formulation. Each new formulation brings not just mathematical convenience but genuine conceptual insight.

In summary, the framework I’ve sketched here is really just an invitation to be more careful about what level we’re actually arguing about.

Most debates in foundations of physics go nowhere because people are talking past each other or are having arguments like people discussing their favorite sports teams.

Once you see the distinctions clearly, you realize that many “deep” disagreements are actually just category errors, while the most interesting questions remain wide open and largely unexplored.

5

The canonical paper on this topic is Possible Kinematics by Henri Bacry and Jean‐Marc Lévy‐Leblond. In a sense, the non-zero cosmological constant could have been predicted much earlier from symmetry considerations.

Modern culture is focused exclusively on questions that can be answered quickly.

In academia, that’s what you can get funding for. Fast questions can be answered within a few weeks. You can then publish a paper. You can start collecting citations. You can present your answer at conferences. This is how you build a career.

But the most important questions can’t be answered like that.

When you can write down a step-by-step plan for how you’re going to answer a question or solve a specific problem, you aren’t doing research but development.

Research means you only have a fuzzy idea of your destination but no clear idea of how you’re going to get there. You’re mostly just following hunches and intuitions. That’s how the biggest leaps forward are achieved.

Development is the execution of a map toward a goal while research is the pursuit of a goal without a map.

Working on questions you can answer fast means you know what you’re doing. And knowing what you’re doing is a sign you’re not pushing into genuinely new territory.

Slowness allows for the exploration of uncharted territory and unexpected discoveries. Johann Friedrich Böttger spent almost a decade trying to find a formula that produces gold. While he never succeeded, a byproduct of his relentless experimentation was the discovery of a process to produce porcelain.

Andrew Wiles worked in secret for 7 years on Fermat’s Last Theorem, publishing nothing. It took Einstein around ten years to write down the foundational equation of General Relativity.

In this sense, when it comes to research, speed should be considered an anti-signal and slowness a virtue.1

How Intelligence Leads Us Astray

Our very definition of intelligence encodes the bias toward speed. The modern definition of intelligence is extremely narrow. It simply describes the speed at which you can solve well-defined problems.

Consider this: if you get access to an IQ test weeks in advance, you could slowly work through all the problems and memorize the solutions. The test would then score you as a genius. This reveals what IQ tests actually measure. It’s not whether you can solve problems, but how fast you solve them.

And it’s exclusively this kind of intelligence that’s measured in academic and IQ tests.

What these tests completely miss is the ability to select problems worth working on and to choose interesting steps forward in the absence of a well-defined problem.

As a result, many people live under the illusion that because their intelligence doesn’t fit this narrow definition, they’re not able to contribute something meaningful.

As the saying goes, “if you judge a fish by its ability to climb a tree, it will live its whole life believing that it is stupid”.

So where does this obsession with IQ come from? Partly from bad science that got repeated until it became truth. In the 1950s, a Harvard professor named Anne Roe claimed to have measured the IQs of Nobel Prize winners, reporting a median of 166. The finding has been cited ever since. But here’s what actually happened: she never used a real IQ test. She made up her own test from SAT questions, had no comparison group, and when the Nobel laureates took it, they scored... average. Not genius-level. Just fine. She then performed a mysterious statistical conversion to arrive at 166. The raw data showed nothing exceptional. But the inflated number is what survived.

Einstein never took an IQ test, but his school records show a B+ student who failed his college entrance exam on the first try. The numbers you see cited are invented. And the few geniuses we do have data on, like Richard Feynman, scored a “mere” 125.

In fact, it’s not hard to imagine how raw processing speed can be counterproductive. People who excel at quickly solving well-defined problems tend to gravitate toward... well-defined problems. They choose what to work on based on what they’re good at, not necessarily what’s worth doing.

Consider Marilyn vos Savant, listed in the Guinness Book of World Records for the highest recorded IQ. What does she do with it? She writes a puzzle column for Parade magazine.

Slow thinkers, on the other hand, have an easier time ignoring legible problems. They’re not constantly tempted by technical puzzles they know they could solve.2

The obsession with processing speed creates a systemic filter. Because we measure intelligence by how quickly one can reach a known finish line, we exclusively fund the ‘sprinters.’ But if you are a sprinter, you have no incentive to wander into the trackless wilderness of true research where speed is irrelevant because the direction is unknown.

At the same time, ‘sprinters’ rise to leadership and design institutions that reward the same legibility they excel at. Over time, our institutions have become nothing but a series of well-manicured running tracks. By rewarding those who can write down and finish well-explained plans the fastest, we have built a world that has no room for anyone who doesn’t yet have a plan.

Illegibility

Legibility and speed are connected. Well-defined problems come with clear milestones, measurable progress, and recognizable success. They’re easy to explain to funding committees, to put on a CV, to defend in casual conversations.

But, as Michael Nielsen put it: “the most significant creative work is illegible to existing institutions, and so almost unfundable. There is a grain of truth to Groucho’s Law: you should never work on any project for which you can get funding.”

Because if it’s fundable, it means the path is already clear enough that it will happen anyway. You’re not needed there.

Many people abandon interesting problems because they don’t know how to defend them and how to lay out a legible path forward. When someone asks “what are you working on?” they need an answer that immediately makes sense. When people ask “how’s it going?” they need visible progress to report. The illegible path offers neither. So most people switch to something they can explain.

And this is how modern institutions crush slow thinkers. Through thousand small moments the illegible path becomes socially unbearable.3

So here is a question worth sitting with: What problem would you work on if you could delete “legible progress within the next ten years” from your list of requirements?

There are no classes on how progress in science happens or how to pick worthwhile research questions.

I guess you’re supposed to pick this up by osmosis or something.

Does this work? No. At best you’ll hear some hushed comment about Kuhn’s paradigm shifts or “The Scientific Method”.

This is a big factor in why there is so little progress.

Virtually all energy and resources are wasted on pointless projects.

This could be avoided if only people spent some time actually thinking about scientific progress in a systematic way and about what questions are actually worth pursuing.

So here’s my attempt to do just that.

What do we actually want?

In a nutshell, we want to find increasingly powerful explanations for how nature works that are backed up by data and logic.

On the one hand, explanations get more powerful when they help us understand something we previously couldn’t. When a new model helps us make sense of a previous unexplained phenomenon, that’s progress.

But on the other hand, explanations get more powerful when they are able to explain the same in simpler ways. A model that provides a unified explanation of dozens of phenomena that previously required different models is more powerful even if it doesn’t explain anything previously unexplained.

A useful way to think about this is in terms of elegance and convergence:1

• Elegance here means “power” or “multi-aptness”. The more domains/levels/phenomena a given explanation illuminates without flattening them, the more elegant it is. Think: few degrees of freedom for many consequences.2

• Convergence means that multiple independent lines of evidence point towards it. So convergence gives us bias reduction and trustworthiness. Think: data and constraints (e.g. mathematical consistency) squeeze it into place. Crucially, convergence is not a static property but it’s a trajectory. Philosopher Imre Lakatos captured this with his distinction between “progressive” and “degenerating” research programs. What matters is the derivative: are new developments tightening or loosening the constraints?
  
  Grand Unified Theories provide a clean example. In the early 1980s, extrapolating the three coupling constants of the Standard Model to high energies showed them nearly meeting at a single point. That’s exactly what you’d expect if there’s one unified force. But as measurements became more precise throughout the 80s and 90s, it became clear that the three lines actually miss each other by quite a bit. The convergence that once made GUTs compelling evaporated.

With this in mind, we can draft a 2x2 chart that will be helpful in understanding models of scientific progress and problem selection.

We call an explanation with the right balance between elegance and convergence plausible.

Plausible doesn’t mean it’s true. It only means it’s worth taking seriously.

At the highest level of elegance and convergence we find ideas that are profound.

For example, Maxwell’s theory of electromagnetism is profound because it provides an elegant explanation of a vast number of phenomena and has a ton of experimental data plus mathematical consistency to back it up.

It’s the gold standard of what we’re trying to achieve in science.

Most explanations do not meet this standard or come even close.

Low convergence and low elegance explanations are usually not worth talking about and we can just discard them as noise.

An inelegant explanation that is backed by a ton of data and mathematical consistency is trivial. With enough structural complexity you can easily explain anything.

The thing about trivial explanations is not that they’re false. But they’re not powerful. Trivial explanations provide little to no insight.

The infamous epicycles, for example, are placed in this quadrant. They are not completely trivial but close.

And lastly, highly elegant explanations with no convergence toward them are what we call conspiracy theories.

This framework might seem trivial (hah) but it will become clear in a minute why it’s worth considering.

To start, note that we need a plausibility framework because our resources and time are finite and hence we can’t do a random search.

We don’t want to test any hypothesis anyone can come up with.

“Cutting my hair will increase the GDP in Burundi.”

“Alphabetizing my spice rack will slow the Lambert Glacier’s melt rate by 0.0001 percent.”

It is obvious in these instances that testing these hypotheses is a waste of time and resources.

Things are less obvious as soon as you start dressing your hypothesis in fashionable, consistent math.

For example, there are infinitely many well-defined quantum field theory models that look just like the Standard Model at low energies. In other words, no current low-energy experiment can disprove them.

Hence without a plausibility filter, you are not doing directed search. You are wasting billions performing a random search inside an infinitely large hypothesis space. But that doesn’t stop researchers from publishing hundreds of papers on such models every year.

Abusing the Machinery

Where things get even more tricky is that people often abuse this machinery to bullshit others and themselves.

They do this by freely oscillating between different ways of presenting their explanations to make them seem more plausible than they really are. This is the famous Motte-and-Bailey strategy.

You first present a strong statement and when people start pointing out problems with it you retreat to a different one that is easier to defend.

For example, what if simply by replacing point particles with strings our theory would become so constrained that we could explain why we observe the elementary particle zoo. That’s an extremely elegant idea that became popular in the 80s. Back then there was reasonable hope that mathematical and experimental convergence would materialize. So String Theory seemed like a plausible explanation worth taking seriously. Now, 40 years later we know that there is no formal convergence. String Theory has a landscape problem with more than 10⁵⁰⁰ ways of constructing string theory models. Also, still zero experimental evidence convincingly pointing towards String Theory. It slowly morphed from a theory of everything into a theory of anything.

But the reason so many people keep working on String Theory is that it can be laundered across quadrants. The original plausible story is used to excite students and the public. When pressed by people who know where the bodies are buried, researchers quickly retreat to safer but less plausible claims in a different corner of the map:

We could also call this faux elegance:

• Bailey (marketed claim): “One simple idea explains everything.”

• Motte (defensive retreat): “Sure it needs a lot of extra clauses, exceptions, knobs, hidden machinery… but the core idea is still ‘simple’ and the math is ‘beautiful’.”

To use again Imre Lakatos terminology: in the 1980s, string theory was progressive: each new result seemed to tighten the constraints. Today it’s degenerating: each new development (the landscape, the multiverse, etc.) loosens them. The trajectory reversed, but the rhetoric didn’t.

There are also much simpler examples of how people abuse our plausibility machinery.

Take the classic example: “The universe is made of information.”

People say this and everybody nods thinking “Oh, that’s very profound…”.

But notice what’s really going on here.

Information is a deep, nuanced concept. So when someone drops an undeniably true statement about it, we feel like we learn something profound.

But in reality, we’ve been given a triviality.

In its trivial reading, the statement is a tautology: any physical state can be described as data. To do physics at all is to map nature onto information. It’s like saying, “A book is made of alphabet.” It’s true, but it tells you nothing about the story.

The “deeper truth” the statement hints at is that the universe is a literal computation or that “bits” exist without a substrate is unsupported by facts.3

Daniel Dennett calls this a deepity. Deepities are statements that are pretending to give you multi-aptness, when in fact what you’re getting is triviality.4

The trick is that a deepity always has two meanings: one that is true but trivial, and another that sounds profound, but is largely unsupported. It’s bullshitting through equivocation. We can also call this pseudo-profundity and it’s another example of the Motte-Bailey strategy.

People like to make these kinds of statements because they are easy to defend. You can always retreat to the trivially true meaning (”I just mean we can use information theory to describe entropy!”) whenever someone points out that the “profound” meaning has no clothes.

The weak anthropic principle is another example of a popular deepity in science. In the trivial reading it just says “we observe conditions compatible with observers,” which is a tautology. In the seductive reading it pretends to explain why the universe has the constants it has, even though it adds no causal mechanism and makes no risky predictions.

Scientific Progress

As I have mentioned before, the standard model of scientific progress is not backed by facts. To use our terminology here, it’s an elegant explanation with low convergence.

But it’s instructive to map it onto our chart and compare it to a more accurate model of progress.

Kuhn’s model of paradigm shifts roughly goes as follows:

• We start with Model A that sits in the upper right corner. It’s highly plausible since it’s sufficiently elegant and backed by mathematical consistency and experimental data.

• But then new experimental data pushes it to the upper left quadrant. No longer all facts converge on the old model. This causes a “model crisis”.

• This crisis is solved when a new model is proposed that is at least as elegant and has the experimental facts converge towards it.

On the other hand, a more accurate model of scientific progress is this:

• We again start with the incumbent Model A sitting in the upper right corner.

• New experimental evidence shows up that is not directly explained by Model A. But instead of pushing the model to the upper left quadrant, researchers quickly add small fixes. A little epicycle here, a new quantum field there. Instead of Model A we are now dealing with Model A*. In other words, researchers maintain convergence by sacrificing elegance. Researchers are usually unwilling to give up models they spent their whole careers mastering.5

• Over time this makes the model less and less elegant. In our chart the model gradually gets pushed down.

• Challenger Model B that eventually replaces Model A**** starts in the upper left quadrant. It’s elegant but has insufficient convergence. After all, it often takes years to work out how a given model explains a given set of experiments.

• If sufficient work is put into testing Model B experimentally and putting it mathematically on solid ground, it slowly starts moving to the right. Eventually it hits a threshold where it’s plausible enough to be taken seriously.

Model Building

Once you have a proper model of scientific progress, it’s clear that most research activity isn’t very promising.

The most common approach is to take the current best Model A and then propose an incremental variation of it, Model A*. This is a safe approach since you will within a predictable time span get to a point where you can write a research paper about your work. You can easily get funding. It is easy to explain and defend since it is so close to the established model. All of these incremental model-building exercises are plausible.

The usual reasoning for this approach is entirely motivated by Kuhn’s faulty model. In short, we have to wait for a proper model crisis caused by new data that will force us to try something more radical. Until then there’s nothing reasonable to do but boring incremental research.

Except that this crisis will never come. Quantum field theory, for example, is a framework so flexible that no matter what you discover in a collider experiment you most likely can accommodate it by adding yet another field to the Standard Model of Particle Physics or add some other minor variation. And if you study the history of scientific discovery or know anything about humans it’s clear that this will always be the preferred, default approach. The scientific community has a tremendous amount of inertia.

However, ideas that elevate our understanding of nature to a truly new level virtually always start in the top-left “conspiracy” corner. They are elegant but lack convergence. New ideas are mere hatchlings that stand no chance in a fight against the full-grown eagle that is the established best model. The incumbent model had many decades to accumulate evidence of convergence. No new model can provide anything close to that right from the start. And it’s not just a lack of experimental evidence but also formal convergence. Typically few of the structural arguments that squeeze it into place have been worked out right away.

This makes it easy to dismiss new ideas. It is always trivial for experts that studied the incumbent model for years to launch devastating attacks against any idea that challenges it.

For example, when Louis de Broglie presented his framework to describe quantum mechanics at the Solvay conference in 1927, he was quickly shot down by guys like Wolfgang Pauli and Hans Kramers. Pauli’s objection was based on a misleading analogy, while Kramers demanded an explanation of a complex phenomenon that de Broglie was unable to provide on the spot. Discouraged by the criticism, de Broglie abandoned his framework. This stalled progress for more than 20 years until David Bohm rediscovered the same approach.

The elegance-convergence model provides a useful lens to understand this dynamic. As outlined at the beginning, our goal in science is of course to find plausible, or ideally profound, ideas.

However, paradigm-shifting ideas are in the technical sense, not plausible right from the start. It’s not “reasonable” to take them seriously. Hence typically no one does.

It requires someone with arational belief, following just a hunch, to propose and defend it.

On the other hand, there is a good reason why the top-left quadrant is labeled “conspiracy theories”. They also belong here. Not every elegant idea deserves to be taken seriously.6

At the same time, not everything that looks like a “conspiracy theory” (aka elegant explanations that lack convergence) should be dismissed right away.7 But unfortunately that’s exactly what happens.

No one is funding risky research on not-yet-plausible ideas in the upper-left corner. Everyone is afraid of being labeled a crackpot. This is an important factor why there is no new Einstein, why scientific progress has slowed down so much.

Just think about how crazy that is. If you spend a little time studying the history of scientific progress, it becomes obvious where most of the energy, time, and resources should be directed. If you spend some time thinking about what we are actually trying to achieve in science, the fallacies become obvious.

And yet, that upper-left corner is mostly an abandoned wasteland that no one is willing to visit.

My hope is that this framework helps a little to think more clearly about where to direct efforts. And maybe to give that weird idea in the upper-left corner a second look before shooting it down.

I.

I still remember how shocked I was when I realized that virtually no one at university was serious about studying physics.

No one wanted to talk about physics beyond what was required to solve homework problems.

Mind you, these were all people that signed up voluntarily to spend at least the next 3 years of their life studying physics.

But everyone acted like this was just a random hobby they picked up yesterday and it didn’t mean anything to them.

People had signed up because society and their parents expected them to do something legible. They didn’t hate physics at school so that seemed like a good option to buy themselves some time.

It certainly didn’t get better the longer I stayed at university.

PhD students, post-docs, and even professors weren’t any more serious about figuring out nature’s secrets.

No one was randomly bringing up insights from papers they just read during lunch breaks. No professor was inviting students to discussions about fundamental questions. If there were ever any discussions, they were about technical details required to finish a specific paper. No one displayed any serious curiosity.

I’m not sure where I got the impression this would be any different. Probably from reading Richard Feynman’s books. But I certainly didn’t feel like this extreme casualness about what should be your life’s work, your craft, was normal or healthy.

II.

Now that I’ve left the academic world behind me for a bit, I’ve realized that this is a much broader societal development.

It’s maybe most obvious in the way people dress now.

No one dresses up for anything anymore except maybe for weddings. Everyone dresses like a slob.

People can’t even fathom why anyone would wear anything that isn’t casual.

When did everyone become so weirdly casual about their life, about their work, about their education, about how they spend their time, about everything?

No one reads serious books anymore.

No one is serious about their hobbies anymore. People’s hobbies nowadays are doomscrolling or watching other people play video games since playing yourself would be too serious.

No one seriously listens to albums anymore. Music is just background noise now. It’s all just AI-curated slob playlists that perfectly blend into the background.

No one seriously watches movies anymore. Netflix is telling writers to dumb down shows since viewers aren’t paying attention. Cinemas are only showing casual fun like Marvel reboots and sequels.

Dating is a cesspool of casualness now.

Serious friendships are becoming increasingly rare.

And just like I’ve discovered in the physics department, no one is serious about their work anymore.

Work consumes a significant part of your life. It defines who you are whether you like it or not. Acting like it doesn’t matter is just weird.

So maybe it’s not surprising that one of the weirdest manifestations of casualness I’ve seen is among entrepreneurs.

Just like with physics, I expected people to be serious, either about solving real problems or at least making a ton of money.

But nope.

Many entrepreneurs nowadays are just “indie hacking”.

They launch little projects, never fully committing to anything, never finding the confidence to truly tell the world what they are building.

No real ambition. No obsession.

III.

If someone watched you for a week, would they think you’re serious about anything?

Why not?

We’ve been sold the idea that casualness is freedom. That not really caring is cool. That commitment is dumb. That keeping everything loose and uncommitted means keeping your options open, staying flexible, remaining free.

It’s of course an oversimplistic explanation but I do think that sitcoms played a major role here. For ten seasons, 52.5 million people watched Ross get mocked every time he tried to share something he cared about. Mid-sentence, his friends would groan, the laugh track would roll, and we all learned: enthusiasm is annoying, intelligence is boring, caring too much makes you the punchline.

That’s brainwashing: the constant reinforcement that earnestness deserves ridicule, packaged as entertainment and beamed into living rooms every Thursday night.

Collectively we’ve learned to keep everything casual as a defensive posture.

But casualness is a cage.

While it keeps you safe, it makes you numb. Watch what happens to people who live this way. They drift through a fog of perpetual optionality, trapped in a diffuse, low-grade anxiety. A nagging sense that nothing really matters, that life is slipping away in an endless scroll of uncommitted half-gestures.

The cage keeps you protected from commitment, from failure, from the vulnerability of actually caring. But that safety is itself a prison.

You’re protected from everything, including living a meaningful life.

The opposite of casualness is seriousness.

Seriousness doesn’t mean you are not having fun.

It just means you actually care. It means prioritizing long-term satisfaction over short-term dopamine.

Real freedom comes from commitment, not from keeping your options open.

The people I know who seem most alive are the ones who take something seriously.

Their work, their craft, their friendships, their hobbies. They’re willing to look uncool, to seem try-hard, to risk actually giving a damn.

They’ve just decided that something is allowed to matter to them.

I.

One of my icks is reading anything that was clearly only written because the author felt like they had to write, not because they actually felt the urgent need to share something.

That includes most books, most news and magazine articles, and research papers.

And you know what virtually all of these have in common? They’re published by professionals.

Professional authors, professional journalists, professional researchers.

It’s weird that the word professional has such a good and the word amateur has such a bad connotation nowadays.

“Amateur” comes from the Latin word “amare” which means “to love”.

“Professional” comes from the Latin “professio”, meaning a public declaration or vow.

In other words:

• Amateur = one who acts out of love

• Professional = one who acts out of declaration or duty

Both are absolutely valid modes of operation.

But it’s complete nonsense that only professionals can produce valuable work.

Especially in professions that require creativity I’d argue it’s rather the opposite.

Professional authors have to publish books regularly. That’s their profession. That’s how they pay the bills. That’s what society expects from them if they want to keep calling themselves professional authors. It doesn’t matter if they feel inspired or if they have any particularly good ideas. They have to sit down and type.

Professional researchers have to publish papers regularly. It doesn’t matter if they actually discovered anything interesting.

Worse, they have to carry out research no matter what. Whether they actually feel inspired to explore a deep question is not a factor.

The main concern is that their research is perceived as professional research in the eyes of their peers and public and leads to publishable papers within a few months.

Compare this to how amateurs operate.

They don’t adhere to any schedule. Society doesn’t expect anything from them.

And this gives them the freedom to actually focus on what matters.

Amateurs can freely follow their creative compass.

They can chase hunches and interesting problems without narrow material and objective constraints.

Quota-driven work kills curiosity.

The best work happens when people are free to have long stretches of no output in service of real discoveries.

II.

Not getting paid doesn’t make your work good.

What matters is why you’re doing it.

Many amateurs fall into the same trap as professionals.

They would love to “turn pro“.

So they try to produce work that will be perceived as professional work.

They sit down, at nine o’clock sharp every morning and write 5 pages.

The result is crap.

Amateurs trying to act like professionals are how unreadable junk books and crackpot papers get published.

Professionals at least have mastered their craft. Their work is mediocre, boring but technically sound.

Another misconception is that being an amateur doesn’t mean you’re just toying around.

Amateurs should be serious about their work.

But it’s the “seriousness of a child at play.“

A third misconception is that you can be a professional operating with an amateur’s mindset.

To win the professional game, you have to care about winning it. That self-selection kills curiosity.

People who once felt the spark to explore deep questions learned to suppress it until they forgot what it felt like. They lost it through attrition.

Exceptions do exist, of course. A tiny number of professionals manage to keep their meaningful work separate from their paid work.

But it’s always weird to read about, for example, researchers who proudly explain that on Sundays they finally have time to think about something interesting.

III.

It’s such a shame that amateurism is virtually dead.

Hardly anyone produces creative work just for the sake of it anymore.

Blogging is dead. Weak replacements like Substack constantly pushes users to put up a paywall. And once you do, you suddenly have to adhere to a schedule to give subscribers their money’s worth. You can’t just vanish for a few months until you have again something noteworthy to share. So you start churning out posts for the sake of it. The quality of your work quickly deteriorates.

Amateur research is dead. Killed by peer review.

Anderson’s “Long Tail” never materialized. Yes, it’s easier than ever to publish a book or research paper. But that abundance quickly backfired. With endless options, readers don’t explore the tail. They cling to the head. No one’s digging through thousands of junk titles to find a hidden gem. Even Google basically gave up digging through the internet’s long tail and started showing primarily results from a handful of big websites.

I wish I could propose any solution. Things aren’t looking pretty right now.

Maybe AI will help.

Once anyone can churn out mediocre, technically sound research papers and books their “value” will go to zero. Hopefully that’s when people will stop acting like they matter.

Amateurs don’t need AI to fill pages with fluff because they have no quota to fulfill.

Typing was never been the bottleneck for progress. Thinking was.

And it doesn’t seem like current AI technology is any real help with that.

To understand why there’s just one fact you need to know:

AI models trained on their own outputs become worse not better.

Why?

Current AI tech is simply producing “blurry JPEGs of the internet“.

And if you keep copying JPEGs of JPEGs, the image decays.

Data is the main bottleneck to make current models better. If synthetic data could improve models, we’d have already hit escape velocity.

What this means is that AI isn’t able to produce original ideas, even though it’s admittedly extremely good at giving the impression that it can.

So maybe AI can help level the playing field.

It could help amateurs close technical gaps and eliminate the formal errors that make their work easy to dismiss.

Maybe that’s how genuine curiosity finally gets a fair shot again.

I.

One thing I always found frustrating is that no one properly explained to me what modern mathematicians do.

A few hundred years ago it was obvious. People did experiments. Other people (or often the same people doing the experiments) invented new mathematical tools to describe what they saw.

Advancements in physics and mathematics went hand in hand.

But at some point both disciplines became increasingly decoupled.

Nowadays most mathematical research activity is largely detached from physics.

One reason is certainly that progress in physics has significantly slowed down. All mathematical tools needed to describe experiments was already invented and well understood.

There was also a vibe shift pushed by guys like David Hilbert towards more abstract mathematics. Abstract mathematics is “more pure“. Hence this is what the smartest minds should focus on.

It took me far longer than I’m willing to admit to understand what games mathematicians are playing now instead.

II.

Here’s an example.

Take an intuitively familiar notion like “symmetry” or “size”.

Then ask: “What even defines a symmetry?” or “What even defines a size?”.

Let’s start with symmetry.

Imagine I’m holding a ball in front of you. You close your eyes. I do something to the ball. You open your eyes. If you can’t tell I did anything, that thing I did was a symmetry.

Rotating the ball? That’s a symmetry since you can’t tell.

Moving it three feet to the left? Not a symmetry since you can definitely tell something changed.

Now we can’t just think about the symmetry of a ball, but also of, say, a square, or a set of balls, or even something more abstract like an equation.

The idea remains the same. When a transformation leaves something unchanged we intuitively can imagine it as a symmetry.

Thinking about this gives you a list of common-sense criteria that all intuitive examples of a symmetry fulfil.

(1) Doing nothing counts as a symmetry.

(2) If you do one symmetry and then another, that’s also a symmetry.

(3) Every symmetry can be undone by another symmetry.

These three rules capture the essence of symmetry. Any transformation that follows these rules counts as a symmetry, even if we can’t easily visualize it.

Now let’s look at “size” the same way.

Let’s take a normal number like 3.

What is its size? “Uh, 3?” you say, looking at me like I’m an idiot.

Okay, what about -5? Is its size -5, or is it 5?

Most people would say 5 since we care about how far from zero it is, not which direction.

This is what your 7th grade teacher called “absolute value.”

Just as for symmetries we can now come up with a list of criteria that captures the essence of what “size” means:

(1) The size of the number 0 is 0, and no other number has size 0.

(2) If you multiply two numbers together, the size of their product is the product of their sizes.

(3) If you add them together, the size of their sum is less than or equal to the sum of their sizes.

Take a moment to verify the familiar absolute value follows these rules. The size of 0? Zero, check. Multiply 3 × 4? Size is 12, which equals 3 × 4, check. Add 3 + 4? Size is 7, which is less or equal than 3 + 4, check. It works.

So far, so boring.

But once we did the boring work of rigorously defining the essence of a common sense notion, we can start to think about what other examples fulfil it besides the intuitive ones we used as our starting points.

Take symmetry first. This is how we discover plenty of strange symmetries beyond the familiar ones that are easily visualized as, say, “rotational symmetry of a ball”.

Like the symmetries described by groups like SU(3) that show up in particle physics, or weirder ones like the exceptional group G2 that has 14 dimensions and no simple geometric picture at all.

Same deal with size.

Here’s one: pick a prime number, p.

Now declare that the “size” of a number is based on the highest power of p that cleanly divides it. So if p is 3, then 18 has “size” related to 9 (which is 3 squared), because 18 is divisible by 9 but not by 27.

Throw in some logarithms to make the rules work exactly, extend it to fractions, and you get the p-adic numbers.

A completely different number system with a completely different notion of what “size” means. Numbers that are close together in the normal sense can be far apart in the p-adic sense and vice versa.

III.

Once we found a few examples we can try to systematize our search.

In the case of symmetries it turns out there is only a finite set.

For notions of size on the familiar numbers, there’s the usual absolute value, the boring one where everything except 0 has size 1, and one p-adic version for each prime. That’s it.

The same pattern shows up everywhere.

For example, once you formalize what it even means to be a “number system” (something where you can add, multiply, and divide (except by zero), and where multiplication behaves nicely with respect to size) you find there are exactly four: real numbers, complex numbers, quaternions, and octonions. This is Hurwitz’s theorem.

So this is one game modern mathematicians play. Take a common sense notion. Formalize it rigorously. Find ALL the strange beasts that technically satisfy your definition. Classify them completely.

That’s what we did with symmetry and size. We wrote down the rules, then asked: what are all the possible things that follow these rules? Sometimes you get a messy zoo. Sometimes you get a shockingly short list.

A secret hope is always that some (all?) of these strange mathematical beasts somehow play a role in nature.

After all, why would nature only make use of some specific narrow slice of mathematical technology?

If it uses real numbers, why not complex numbers too?

Oh wait, it actually does in quantum mechanics.

So what about quaternions and octonions?

Maybe a strange symmetry like E6 or E8 (related to octonions) describe some undiscovered fundamental symmetry of nature.

Maybe p-adic numbers is exactly the mathematical technology we need to finally make sense of quantum mechanics?

Why would the universe be weirdly conservative, only employing specific mathematical structures, when all these other wild possibilities exist?

Maybe it wouldn’t be. Maybe it uses all of them and we just haven’t found where yet.

IV.

There is a second related game mathematicians play.

Once we’ve written down a list of criteria that define a “thing” we can also ask: what if we relax one of these assumptions?

The historical precedent that motivates why this makes sense is Non-Euclidean geometry.

For thousands of years, Euclidean geometry was just common sense. Parallel lines never meet. The angles in a triangle add up to 180 degrees. The shortest distance between two points is a straight line.

Then mathematicians started asking: what if we drop the parallel postulate? What if parallel lines could meet?

Turns out when you do this you get hyperbolic geometry, spherical geometry, and all sorts of other weird spaces.

Then Einstein shows up decades later and realizes these weird structures is exactly what we need to describe gravity.

Riemann’s abstract mathematical game from the 1850s became the language of general relativity in 1915.

With this in mind it seems natural to push further.

What if we relax the assumptions built into Riemannian geometry

You can study geometric frameworks that have torsion, or that aren’t metric-compatible, or both.

What if spacetime has torsion? What if it has non-metricity?

So in this optimistic view, mathematicians are systematically exploring the full landscape of mathematical possibility.

Classifying everything that can be classified. Relaxing every assumption that can be relaxed. Building the complete atlas before physicists show up needing a map.

V.

Do these mathematical games ever end?

Can we classify all the things that can be classified? Is there a structured way to think through all the ways assumptions can be dropped?

Well, there’s category theory.

Once you’ve classified all the symmetries, you can study the structure of how symmetries relate to each other.

Once you’ve found all the number systems, you can study how they map into each other.

The relationships between mathematical objects are themselves mathematical objects you can formalize and classify.

And once you understand those patterns, you can classify entire “mathematical universes” with different internal rules.

This is topos theory, where even basic logical laws might work differently.

In other words, you can study what happens when you relax the assumptions at the very heart of mathematics.

At what point do these games stop being useful and start being silly?

No clue.

The only thing that for sure seems silly is trying to predict what mathematical tool will end up being useful to describe nature.

Doesn’t mean all of it will be useful.

But a ton that seemed silly ended up making sense. So mathematics will most likely remain unreasonably effective.

Moreover, leaving physics aside, there is also the hope that if you keep pushing the frontier of abstraction, you’ll eventuell reach at the “heart of hearts“.

Some fundamental layer where everything just clicks. Where all the strange coincidences and mysterious connections between different areas of math finally make sense because you’re seeing things the right way.

Whether that exists, nobody knows.

But it definitely feels like it should, just like a more unified framework of fundamental physics.

And I can totally see how someone might go crazy by repeatedly banging their head against that final abstraction ceiling for too long.

In the past few weeks, I've gone down what you might call the quantum foundations rabbit hole - talking to a dozen researchers and reading enough papers to fill a small library. What I found was... concerning.

Imagine you're learning a new language, except everyone who claims to speak it has their own private dictionary. And instead of helpful corrections, you get drawn into ancient blood feuds about whether "mesa" means "table" or "tablecloth" or possibly "the experience of eating at a table."1

This is roughly what it's like trying to understand quantum foundations research in 2025.

The field has splintered into a dozen different dialects, each with its own interpretation of basic concepts. It's as if we've spent ninety years having a debate where everyone is talking past each other so completely that we can't even agree on what we're disagreeing about.2

As Sabine Hossenfelder puts it, "The major problem with quantum mechanics, it seems, is that we can't agree what the problem is."

This would be merely amusing if we weren't still struggling with the same foundational issues - quantum gravity, dark matter - that researchers a century ago did.

It seems unlikely that any progress is possible until this mess is properly cleaned up.

Here are a few ideas on how we might start to sort this out.

Interpretations, formulations, modifications, and nonsense

“If God is a mathematician, in what dialect does She/He/They/It speak?” - John Horgan

The difference between interpretations, formulations, modifications and plain old nonsense has to be crystal clear.

You can formulate quantum mechanics in Hilbert space, phase space, configuration space, or real space. Some calculations are easier in one formulation but that doesn’t mean it’s more correct. As long as the mathematical map between them is sound, they are equivalent.

This is completely analogous to the situation in classical mechanics. For many problems, the standard Newtonian formulation in real space is perfectly fine. But formulations like the Lagrangian one in configuration space or the Hamiltonian one in phase space are more convenient for a certain class of problems. And if you want to carry out calculations in Hilbert space, you can use the Koopman-von Neumann formulation. Each formulation has its merits, but they're mathematically equivalent.

There is absolutely nothing controversial about this.

And yet virtually all work is done using the Hilbert space formulation, while other formulations like the Bohm-de Broglie formulation are still largely ignored for mostly sociological reasons.3

People often point out that most calculations can only be done using the Hilbert space formulation. This, however, ignores the obvious fact that approximately 1000x more manpower so far went into developing the necessary calculation tools for the Hilbert space formulation. If, say, the Bohm-de Broglie formulation had been discovered before the Hilbert space formulation, the situation would probably be reversed. Physicists might now be arguing that the Hilbert space formulation is too abstract and complicated compared to the more intuitive Bohm-de Broglie approach.

Modifications, on the other hand, actually alter the theory's mathematical structure and predictions. Examples include collapse models like GRW theory . These aren't just different ways of looking at quantum mechanics - they're genuinely different theories that can be tested experimentally.

Last but not least, interpretations provide different philosophical frameworks for understanding what the mathematical formalism means. They don't change the mathematics or predictions, but rather offer various metaphysical perspectives on what's "really" happening. The Many-Worlds interpretation and QBism are examples of different ways to philosophically interpret the same underlying mathematical structure.

Different formulations certainly might hint at different interpretations.

But if anything, the fact that we have multiple equivalent formulations should give us pause when considering any single interpretation too dogmatically.

Again, this is no different from the situation in classical mechanics.

Most straightforwardly, we can look at classical mechanics as a framework describing inert objects pushed around by forces. We can also interpret it by observing that Nature seems to be driven by a desire to extremize the Action. You could certainly also cook up an interpretation by staring long and hard at Hamilton’s principal function.

But there is no reason to claim that any of these points of view is more correct than another.

Most importantly, no one should get confused by nonsense like the “Copenhagen interpretation,” which really doesn’t deserve to be called an interpretation at all. It’s a collection of vague philosophical statements that don’t make much sense no matter how long you stare at them.4

In summary, these four categories - formulations, modifications, interpretations, and nonsense - serve distinct purposes and shouldn't be conflated.

Instead of fighting against each other like fans of different sports teams, researchers should focus on building bridges between different formulations and leveraging each one's unique strengths for different types of problems.5

Modifications deserve to be tested, interpretations to be discussed but not dogmatically held, and nonsense to be ignored.

“There is a pleasure in recognizing old things from a new point of view […] there is always the hope that the new point of view will inspire an idea for the modification of present theories, a modification necessary to encompass present experiments.” - Richard Feynman

Put genuine quantum weirdness into the spotlight

While most researchers do agree that quantum mechanics is weird, there’s hardly any agreement on what exactly is weird about it.

Virtually all examples of fundamental quantum weirdness (randomness, discreteness, the indistinguishability of states, measurement-uncertainty, measurement-disturbance, complementarity, non-commutativity, interference, the no-cloning theorem, and the collapse of the wave-packet) do “appear within classical statistical mechanics under reversible dynamics”.6

The one genuinely strange aspect of quantum mechanics is the experimentally observed violation of the Bell inequalities.7

And yet, there is widespread confusion on what this actually tells us about the world.

The Nobel Prize committee, for example, in their announcement of the 2022 prize, claimed that it shows “that quantum mechanics cannot be replaced by a theory that uses hidden variables.”

This is pretty much the exact opposite of what most researchers would describe as the lessons we learn from Bell-type experiments.

To quote Tim Maudlin in a recent conversation with Sean Carroll:

“The Nobel committee blew it in their press release. They said that what they had done was what proved that von Neumann was right and you can't have hidden variables. The irony there is so delicious. Because Bell became probably the strongest advocate of Bohm's theory or De Broglie's theory, which is a theory with additional variables.”

The different options for understanding the observed violation of Bell’s inequalities need to be spelled out in crystal clear terms and discussed undogmatically.8

Right now, potentially interesting options are being overlooked for sociological reasons. For example, violations of statistical independence are dismissed by invoking John Bell’s claim that this would imply “the complete absence of free will”.

Progress is possible

The situation reminds me of the famous parable of the blind men and the elephant. Each man feels a different part of the animal - the trunk, the tail, the tusk - and becomes absolutely convinced they know what they're dealing with.

The man at the trunk insists it's a snake, the one at the tail swears it's a rope, and they all end up in heated arguments about who's right.

In quantum mechanics, we have Bohmians, Many Worlders, relationalists, QBists - each group exploring a different piece of the same puzzle. And just like in the parable, each group has stood in their corner for so long, clutching their piece, that they've forgotten they were all originally trying to describe the same beast.

On top of that, we have mathematicians approaching the problem from yet another direction. They often seem determined to make quantum mechanics sound as unremarkable as possible - as if they're embarrassed by its weirdness. But that's like trying to make Alice in Wonderland "benignly humdrum" by translating it into an axiomatic system.

You haven't explained the talking cats and size-changing potions; you've just hidden them behind a wall of symbols.

The genuinely strange features of quantum theory — like the violation of Bell inequalities — aren’t made any clearer through these approaches. If anything, they become even more confusing.

At the same time, there are tons of beautiful, deep hints where a little bit more attention from people thinking mathematically could help a lot.9

Progress in quantum foundations has been glacially slow for the past century, but it doesn't have to be.

The evidence suggests we're being held back more by human factors than physical ones. Many promising ideas were abandoned not because they failed, but because of historical accidents or personality conflicts.10

Maybe what we need isn't yet another interpretation of quantum mechanics.

Maybe we need something more like couples therapy for physicists - a way to get everyone in the same room, speaking the same language, and remembering why they fell in love with these puzzles in the first place.11

Tons of famous scientists emphasize the importance of aesthetics.

For instance, Murray Gell-Mann:

“We have this remarkable experience in this field of fundamental physics that beauty is a very successful criterion for choosing the right theory.”

Henri Poincaré:

“The scientist does not study nature because it is useful to do so. He studies it because he takes pleasure in it, and he takes pleasure in it because it is beautiful. If nature were not beautiful it would not be worth knowing, and life would not be worth living. I am not speaking, of course, of the beauty which strikes the senses, of the beauty of qualities and appearances. I am far from despising this, but it has nothing to do with science. What I mean is that more intimate beauty which comes from the harmonious order of its parts, and which a pure intelligence can grasp.”

Jim Simmons:

“Be guided by beauty. I really mean that. Pretty much everything I’ve done has had an aesthetic component, at least to me.

Paul Dirac:

"It is more important to have beauty in one's equations than to have them fit experiment."

Hermann Weyl:

"My work always tried to unite the true with the beautiful; but when I had to choose one or the other, I usually chose the beautiful."

Richard Feynman:

“You can recognize truth by its beauty and simplicity.”

Subrahmanyan Chandrasekhar:

"I would like to suggest that in science, as in art, the sense of beauty is the sense of the appropriate or the fitting. And from this point of view, the pursuit of science is simply the pursuit of elegance, or aesthetic satisfaction."

On the other hand, every time researchers try to formalize this idea and use it as a guiding principle things go horribly wrong.1

Formalizing beauty

The most common ways to formalize what beauty in science mean are: symmetry and naturalness.2

The study of more symmetric or even supersymmetric models has, so far, turned out to be a dead end.

One issue is that there’s an infinite number of ways to make the current best model of nature at fundamental scales more symmetric. Literally.

For example, you can embed the “ugly” gauge symmetry of the standard model SU(3) x SU(2) x U(1) in SU(5) and then argue this symmetry breaks down at higher energies into the puzzle pieces we observe at energy scales we can currently probe.

But you can also embed it into SU(6), SU(7), SU(8) or SU(9999). Or you can embed it in SO(10), SO(14), SO(18), or SO(998). Or you can embed it in E(6), E(7), or E(8).

There are infinitely many options. The story is always the same. All the extra stuff decouples at sufficiently high energies and what we are able to observe at low energies is SU(3) x SU(2) x U(1).

Similarly, there are infinitely many family symmetries you can invoke to unify the three generations of elementary particles.3

Adding the requirement of “simplicity” isn’t of much help either.

The minimal grand-unified model based on SU(5) predicts that protons should decay at a rate above the current experimental threshold. In other words, it’s ruled out by experiments.

Another idea is to augment symmetry by hinting at a vague requirement of “exceptionalness”. To quote, Ed Witten:

Describing nature by a group taken from an infinite family does raise an obvious question – why this group and not another? In addition to the three infinite families, there are five exceptional Lie groups, namely G2, F4,E6,E7, and E8. Since nature is so exceptional, why not describe it using an exceptional Lie group? […] The grand unified theory based on E6 is not clearly superior to the SO(10) model, but it does capture the successes of the SO(10) model “exceptionally.”

This seems like an even weaker argument.

On the other hand, if we take another look at the standard model gauge group it doesn’t seem that bad at all. SU(3) x SU(2) x U(1), while not a “simple group”, has a nice 1-2-3 ring to it and it’s definitely perfectly suitable for a minimal model that is able to describe what we observe in collider experiments.

Symmetry is undoubtedly beautiful but there is no way to rank different symmetries in terms of their aesthetic value.4

Arguments that our models of nature should be “natural” run into similar issues.

First of all, calling anything that we observe "unnatural" is an oxymoron.

Have a look at the Borwein integrals below.

The breakdown of the pattern is undeniably ugly.

But that doesn’t mean it’s wrong.

Secondly, naturalness was the primary reason why many particle physicist were convinced new particles besides the Higgs boson would show up in LHC detectors.

Well, that didn’t happen.

Various measures of naturalness have been invented to argue for and against different models.

Hundreds of papers have been published that propose solutions to the various “naturalness problems” in modern physics (hierarchy problem, flatness problem, baryon asymmetry, strong CP problem).5

There is zero evidence that any of these solutions are actually realized in nature.

So just as symmetry arguments, naturalness has proven to be an unreliable guide for scientific discovery.

In this sense, Sabine Hossenfelder isn’t wrong when she argues that “aesthetic criteria have become a source of cognitive bias leading physics astray”.

This seems pretty weird, right?

On the one hand, so many famous scientist emphasize the importance of beauty in in scientific theories.

On the other hand, all attempts to formalize this idea have led us nowhere.

Here’s how I think the paradox can be resolved.

Effective aesthetics

The beauty that famous scientists talk about is an incompressible concept that can't be turned into a simple algorithm for choosing theories.

Instead, what they describe is related to the idea that big breakthroughs are often the result of someone following hunches and intuitions.

Successful researchers were often simply guided by a general sense of what felt right to them.

Therefore, beauty as a successful guiding principle in science has little to do with easily definable concepts like symmetry or naturalness.

These are just notions people use in hindsight.6

To explain the difference between these different interpretations of beauty as a successful guiding principle let me quote what I wrote about the game Picbreeder.

Picbreeder is a website that allows users to “breed” evolutionary art.

You can select images you like and the system then uses a genetic algorithm to breed new art.

It works analogously to breeding horses except that instead of choosing animals to breed, you choose pictures.

Say all experts agree that breeding the picture of a skull is the top priority right now. […]

Experts develop a test to measure the skull-ness of any candidate picture on a scale from 0 to 100.

Only images that show clear progress towards skull-ness are selected. All other images are discarded.

Will this effort succeed?

Almost certainly not.

Look at this sequence of images that actually generated an image of a skull.

None of the intermediate steps would have passed the skull-ness rating test.

In Picbreeder the most interesting images emerge whenever players follow their hunches and intuitions about what looks most interesting at every step.

Whenever you force to generate a certain type of image, you will almost certainly fail.

With this in mind, it’s hardly surprising that attempts to “breed” a beautiful theory by applying criteria like symmetry or naturalness fail.7

To be clear, the next paradigm-shifting theory in physics will be beautiful.

But I very much doubt that whoever discovers it will find it by applying criteria like symmetry or naturalness.

In fact, a theory's beauty is often only recognized long after its initial discovery.

The beautiful, deep symmetry hidden in Mawell’s theory of electrodynamics, for example, was only fully appreciated decades after Maxwell published his equations.

And yet, scientists will rightfully keep emphasizing the importance of beauty as a guiding principle.

We just need to remember that this is code for following unexplainable intuitions and hunches rather than a rigid criterium.

Without irrational preferences scientific progress grinds to a halt.

There is an infinite number of theories that are perfectly compatible with all known data. Hence it’s impossible to systematically explore the full space of theories.

Moreover, applying measures like symmetry or naturalness are more likely than not leading us down dead ends.

Scientific progress requires that someone develops what will seem to everyone else like an unreasonable preference.

They typically can't fully explain their preference or defend it against all initial attacks. The best they can often do is say "it’s beautiful”.

Most of these aesthetic preferences will indeed turn out to be completely unjustified.

But the good thing about science is that, in the long run, the bad stuff doesn’t matter at all.

All that matters is that eventually one aesthetic hunch will be proven correct.

The following quote by Donald Knuth has always resonated with me:

“Email is a wonderful thing for people whose role in life is to be on top of things. But not for me; my role is to be on the bottom of things.”

I’m not so much against email but very much against trying to stay on top of things.1

Trapped in the Never-Ending Now

“I’m not interested in your new work. I wanna see your best work.”

- Jerry Seinfeld

Humans have a well-documented recency bias.

Watching a football game happening right now feels exciting.

Watching the recording of a game that happened last week feels like chewing stale gum.

If you see someone scrolling social media, virtually everything they look was produced within the last 24 hours.

If you see someone reading a newspaper, it was almost certainly published that day.

If you see someone listening to a podcast, it’s likely a brand new episode released that week.

If you see someone watching a movie or a show, it's usually something brand new.

If you see someone reading a book, it’s probably something written, at most, a few months ago.

People prefer fresh content and all platforms happily optimize their algorithms to serve it.

As a result, everyone is trapped in a Never-Ending Now.

The Lindy argument

The desire to stay on top of things seems hardwired into our psychology.2

And yet, once you take a step back, it all seems pretty insane.

The endless cycle of ephemeral content feels exciting in the moment but is quickly forgotten.

What are the odds that something produced recently will stand the test of time?

How likely is it that any of the new stuff is better than the best works humanity has produced over centuries?

Research on the Lindy effect tells us: not very likely.

“If a book has been in print for forty years, I can expect it to be in print for another forty years. But, and that is the main difference, if it survives another decade, then it will be expected to be in print another fifty years. This, simply, as a rule, tells you why things that have been around for a long time are not "aging" like persons, but "aging" in reverse. Every year that passes without extinction doubles the additional life expectancy. This is an indicator of some robustness. The robustness of an item is proportional to its life!”

- Antifragile by Nassim Nicholas Taleb.

Reading at the level you want to think

“If you only read the books that everyone else is reading, you can only think what everyone else is thinking.” - Haruki Murakami,

Common advice for writers is to read at the level you want to write.

Before writing anything, read a chapter written by someone who writes the way you would like to write.

This, in my experience, works exceptionally well.

A related observation that I've found equally valuable is to read at the level you want to think.

When I read stuff written by shallow thinkers, my thoughts remain shallow.

When I read works by deep thinkers, my thinking naturally deepens.

My mind adapts to match the complexity and depth of the material I consume.

Popular content is easily accessible by definition and hence tends to be simplified and watered-down.

This is why the content you will be served by default is shallow.

Don’t live in the present

Read good writing, and don’t live in the present. Live in the deep past, with the language of the Koran or the Mabinogion or Mother Goose or Dickens or Dickinson or Baldwin or whatever speaks to you deeply. Literature is not high school and it’s not actually necessary to know what everyone around you is wearing, in terms of style, and being influenced by people who are being published in this very moment is going to make you look just like them, which is probably not a good long-term goal for being yourself or making a meaningful contribution. At any point in history there is a great tide of writers of similar tone, they wash in, they wash out, the strange starfish stay behind, and the conches. Check out the bestseller list for April 1935 or August 1978 if you don’t believe me. Originality is partly a matter of having your own influences: read evolutionary biology textbooks or the Old Testament, find your metaphors where no one’s looking…

- Rebecca Solnit

A few clicks away

Just like Donald Knuth, I have no interest in trying to stay on top of things.

Instead, I'm trying to get to the bottom.

And it only takes a few clicks to access the best works humanity has ever produced.

So why am I wasting my time reading mediocre “top of things” content?

This struck me when I was doing some reading on scientific creativity recently.

In one blog post, Maria Popova quotes from a book by Jacques Hadamard, who surveyed guys like Albert Einstein, George Polya, and Claude Lévi-Strauss to understand how they came up with ideas.

Jacques Hadamard himself was a Tier 1 mathematician. This book undoubtedly would contain deeper and more interesting insights than anything Amazon's or Google’s algorithm would serve me when I type in "creativity" or "scientific thinking."

There are more deep books like this out there than I could ever read.

Books like Ideas and Opinion by Albert Einstein are not just worth reading, but worth returning to again and again.

A ton of books, like, for example, Henri Poincaré’s Foundations of Science are freely available online.

A fantastic starting point to find more timeless works is this list of 100 Books that shaped a Century of Science American Scientist published a while ago.

I just need to remember that I have the option to ignore the freshly produced content algorithms shove right in front of me and seek out timeless works that have proven their worth over decades.

To make sure I don't forget, I just placed a little sticky note on my desk that says:

“How about you read some Einstein instead?”

The most common explanation for the slowdown in scientific progress is that we’re running out of low-hanging fruit.

Most easy discoveries have already been made. What’s left is increasingly complex and requires steadily increasing investments in equipment, personnel, and research infrastructure.

For example, physicist Leo Kadanoff states:1

"The truth is, there is nothing — there is nothing— of the same order of magnitude as the accomplishments of the invention of quantum mechanics or of the double helix or of relativity. Just nothing like that has happened in the last few decades. [...] Once you have proven that the world is lawful to the satisfaction of many human beings, you can’t do that again."

It’s a plausible explanation. It’s definitely a convenient one.

If the slowdown is inevitable, there is no one to blame and everyone can just keep going without making any changes.

But I think it’s completely wrong.

The idea that there are few easy discoveries that still can be made hinges on a faulty mental model of knowledge and a misleading interpretation of data.

First of all, knowledge is not finite but fractal. The idea that discoveries necessarily get harder over time because we’ve already explored all easily accessible areas is incorrect. Each new discovery opens up vast new areas, each bringing its own set of low-hanging fruit.

Secondly, scientific discoveries are rarely made as soon as they’re theoretically possible. Hence, it’s nonsense to conclude that data showing a lack of progress despite increased investments implies we’ve run out of low-hanging fruit. There are plenty of alternative interpretations that are just as plausible.

Let’s talk about these two points one after another.

Knowledge is fractal, not finite

Think about a wedding dessert buffet. Early guests grab the best pieces, and by the end of the night only crumbs and sad-looking cookies remain. The “low-hanging fruit” view of science assumes the buffet works this way: a fixed tray, picked over until nothing good is left.

But what if science is a buffet that keeps getting refilled? Every time someone clears a tray, the kitchen rolls out something new, often better than what came before. They wheel out a cheese table nobody knew existed, and next to it a coffee bar, and somewhere in the back someone starts making crepes to order. Each table has its own fresh pile of best pieces waiting to be grabbed first.

The guests who showed up in 1890 thought the good stuff was gone. Then quantum mechanics arrived, and with it quantum chemistry, and solid state physics, and eventually the transistor and the laser and a dozen other tables no one at the original buffet could have imagined.

Knowledge isn’t like a finite landmass waiting to be mapped. It’s more like a fractal pattern that reveals new areas the closer you look. Each discovery doesn’t just fill in a blank spot, it opens up entirely new territories of investigation.

If anything, the blank spots are only getting larger as our scientific understanding expands.

Maxwell’s theory of electrodynamics filled out a huge blank spot in our understanding of physics, but it also contained little bridges to a vast new areas called Special Relativity and Quantum Field Theory.

Our understanding of fundamental physics has simultaneously never been greater and more incomplete.

A century ago, people were pretty sure that the fundamental constituents of matter were atoms. Then we discovered protons, neutrons, and electrons. This led to a whole zoo of “elementary particles”.

Nowadays, we aren’t even sure whether “there are no particles, there are only fields” or only particles and no fields.

Unlike a century ago, there is no coherent framework describing all known fundamental “forces.” This hints at a giant new framework waiting to be discovered.

94% of the universe’s energy content is “dark stuff.” Aptly named because we currently have absolutely no idea what it is.

What once seemed like a fairly well-understood smooth territory has turned into a highly fragmented landscape of poorly understood areas.2

And yet newly discovered theories aren’t necessarily getting more complicated. There are crazy complicated things in Classical Mechanics just as there are crazy complicated stuff in Quantum Field Theory. But at their heart, both theories are similarly simple.

So I don’t see any reason why the fruit in not yet explored territories should be hanging any higher.

And that’s, of course, just fundamental science.

The expansion of areas that can be explored by scientists is even more obvious when we talk about applied science.

Quantum mechanics alone spawned dozens of new fields like quantum computing and quantum cryptography.

Each newly discovered area in the landscape of scientific knowledge contains its own set of unexplored territories and low-hanging fruit.

In addition, if anything, discoveries should become easier thanks to technological progress.

Nowadays, every human with a smartphone has access to all of humanity's accumulated knowledge. With just a few clicks you can access virtually any paper and book ever written. You can run giant simulations and complex calculations on laptops that cost just a few hundred dollars. Anyone willing to invest $20/month now has access to their own personal Marcel Grossman to point them in the right direction whenever they get stuck.

So if it was really true that discoveries are rarer because they are getting harder to find, we should have seen an avalanche of progress as a result of this technological progress.

To stick to our analogy, think of explorers who complained for decades that they couldn't make major discoveries because they lacked proper resources to reach remote areas. Then, suddenly, they got access to drones, advanced mapping technology, and satellite imagery – and they still failed to make any significant discoveries.

This would clearly suggest that it wasn’t difficulties in reaching remote areas that was holding them back in the first place.

Hindsight Bias

Throughout human history, it always took shockingly long to make “obvious” discoveries.

It took thousands of years after the invention of the wheel before someone thought to attach wheels to luggage or before someone invented the bicycle.

Quantum mechanics could have been discovered much earlier by someone attempting to generalize probability theory.

It took thousands of years before someone dared to explore geometry without Euclid's fifth postulate seriously.

Fruit picked in the past always seems a lot more low-hanging than it really was.

Many calculations that are nowadays done by students in a few hours took the first researchers who did them many weeks, if not months.

Knowing that there is a solution, that it's worthwhile to carry out the calculation at all, and a few hints how to approach it go a long way.

Hindsight bias is a well-documented psychological phenomenon.

In one famous experiment, Daphna Baratz (1983) gave college students pairs of "discoveries", one true (for example, "In prosperous times people spend a larger proportion of their income than during a recession" or "People who go to church regularly tend to have more children than people who go to church infrequently"), the other its opposite ("In recession times people spend a larger proportion of their income than during prosperity" and "People who go to church infrequently tend to have more children than people who go to church regularly.")

The result? Whether given the true discovery or its opposite, most students rated it as something “I would have predicted.”

So it’s very much possible that there are plenty of discoveries waiting to be made right now that will seem perfectly obvious in a few decades.

Reality of scientific progress

A second reason why most discoveries were made much later than you would have expected is that progress is not a straightforward process.

Societal factors play a huge role.

This is illustrated, for example, by Max Planck’s observation that “a new scientific truth does not triumph by convincing its opponents and making them see the light, but rather because its opponents eventually die and a new generation grows up that is familiar with it”.

In other words, “science progresses one funeral at a time”.

If scientific progress was a straightforward, rational process, new theories should be widely accepted as soon as sufficient evidence is presented. Instead, established scientists often resist new ideas, regardless of their merit.

There is a fundamental inertia that makes scientific progress slower than it could be.

Just consider how long it took for the mathematical concept of zero to be accepted.3

A more optimistic version of Planck’s principle is Graubard’s Principle: Science progresses one birth at a time.

Often we have to wait for the right person to enter the field with a healthy dose of naivety and unwarranted confidence before the next breakthrough can be achieved.

The following old joke illustrates this nicely:

A finance professor and a student are walking across campus. The student sees a $20 bill on the ground and says, "Look, there's a $20 bill!"

The professor keeps walking and replies, "That can't be a real $20 bill; if it were, someone would have picked it up already."

There are plenty of $20 bills lying around in science today, waiting for the right person to pick them up.

How else can we understand the regular occurrence of anni mirablis where multiple groundbreaking discoveries are made in rapid succession by the same person?

In each instance, there was clearly plenty of low-hanging fruit, but it took the right person to come along to pick it.

For example, Galileo Galilei’s discovery that objects of different weights fall at the same rate or that constant motion is indistinguishable from rest could have been made (or accepted) centuries earlier.

Alternative explanations

With this in mind, it’s clear why an observed slowdown in progress despite increased investments by no means implies that we’ve run out of low-hanging fruit.

There’s no reason to believe that scientific inertia as a cultural phenomenon remains equally strong over time.

What if recent changes in the culture of science, like the introduction of peer review and the fixation on measurable authority increased scientific inertia significantly?

What if we made it harder and harder for new people to participate by professionalizing the job of a scientist, decoupling science from the rest of society, and only funding older researchers instead of giving young researchers opportunities to pursue their own ideas?4

What if attempts to make research funding more efficient made it impossible to explore the most promising stepping stones?

What if the current academic system only supports hill climbers and kicks out all valley crossers?

What if modern technology and increases in bureaucratic processes made it virtually impossible for researchers to dedicate significant time to deep, focused work required for breakthrough insights?5

Pessimism vs. optimism

One of the biggest turning points in my life was the realization that intelligence and talent are vastly overrated.

Through many years of brainwashing in the school system, I believed I wasn’t ever able to do anything meaningful because I was never the smartest or most talented in the room.

But one day I understood how silly believing this is.

All you’re accomplishing is turning it into a self-fulfilling prophecy.

You always have a choice between being optimistic or pessimistic.

Pessimism means you will definitely be correct because you won't even try.

Only by being optimistic are you giving yourself a chance to succeed.

The same applies to scientific progress.

If we believe we've almost reached the end of science or that all the easy discoveries have been made, our prediction almost certainly becomes true.

We will keep putting all focus and resources onto increasingly specialized research and mega experiments. Hence, all discoveries will be increasingly difficult and expensive to make. This self-fulfilling prophecy will reinforce the belief that science has reached its limits.

But if we remain optimistic and keep searching for those "$20 bills" lying around, we might just find them.

Crucially, this is not an exercise in wishful thinking.

As I have laid out above, there is plenty of good reason to believe that major low-hanging scientific breakthroughs are still possible.

Researchers thought they had reached the end of the road already a century ago.

Max Planck was told by a professor around 1890 that “the system as a whole stood there fairly secured, and theoretical physics approached visibly that degree of perfection which, for example, geometry has had already for centuries.”

Or as physicist Albert A. Michelson famously noted, “it seems probable that most of the grand underlying principles have been firmly established and that further advances are to be sought chiefly in the rigorous application of these principles to all the phenomena which come under our notice. It is here that the science of measurement shows its importance — where quantitative work is more to be desired than qualitative work. An eminent physicist remarked that the future truths of physical science are to be looked for in the sixth place of decimals.”

Then guys like Albert Einstein, Werner Heisenberg, Erwin Schrödinger, and Austin Bradford Hill came along and discovered plenty of low-hanging fruit.

It seems naive to believe that this time it's any different.

Do I know for sure? Of course not.

But looking at the evidence and given the choice between optimism and pessimism, I choose optimism every time.

Picbreeder is a website that allows users to “breed” evolutionary art.

You can select images you like and the system then uses a genetic algorithm to breed new art.

It works analogously to breeding horses except that instead of choosing animals to breed, you choose pictures.

What’s fascinating about the system is how unpredictable the evolution of images is. The most interesting images are the result of completely unexpected mutations.

Stepping stones rarely resemble the final product. For example, the eyes of an alien face turn into the wheels of a car.

In fact, when you’re trying to breed, say, the image of a car, you will most likely fail.

Your best chance of breeding an interesting picture is by picking the most interesting pictures at each step without trying to force a specific outcome.

Here’s how the creators of the software describe this unexpected learning: “We noticed that Picbreeder users make their best discoveries if those discoveries aren't their objective. These successful users were instead following their instinct towards the interesting and novel.”

In every instance where users ended up with an interesting final image, they had to go through a series of seemingly unrelated images.

It turns out that this is a fantastic toy model to understand how progress happens in the real world.

Breakthrough discoveries are virtually never the result of a sequence of steps anyone could have predicted.

There’s a great BBC series called Connections where historian James Burke traces how seemingly unrelated discoveries and inventions throughout history led to breakthroughs.

The mechanical loom made linen abundant, leading to cheaper paper production. This enabled book printing, which helped spread information about automated organs using pegged cylinders. French silk weavers adapted this cylinder concept, creating perforated cards to control their looms. Later, similar punch card technology enabled faster census counting, which ultimately influenced early computer design.

It turns out that progress in real life does not follow a clean, causal tech tree as games like Civilization suggest.

Sure, you can connect the dots in hindsight. But absolutely no one could have predicted how all of this would eventually come together.

Here’s another example.

If scientific progress followed strictly rational paths, the anomaly observed in Mercury’s movement should have led to the discovery of General Relativity.

But it didn’t. Instead, scientists stuck to the state-of-the-art theory of Newtonian gravity and “fixed” the model by adding a new planet.

And even though this hypothetical planet called Vulcan was never discovered, no one used this as a starting point to abandon Newtonian gravity and come up with a better theory.

It took a weird guy called Albert Einstein thinking about how he would feel in a falling elevator to trigger the next breakthrough.

One key to understanding why the paths of progress are so unpredictable is that a healthy dose of irrationality is often a necessary condition for breakthroughs.

Irrationality implies unpredictability.

This has important implications for anyone thinking about how to accelerate progress and innovation.

If progress is fundamentally unpredictable, it’s clear why most attempts to manage it make it worse.

Let’s return again to the Picbreeder game.

Say all experts agree that breeding the picture of a skull is the top priority right now.

Hence, the government launches a huge initiative aimed at skull image generation. They establish strict metrics and require detailed plans outlining how the goal can be achieved.

Experts develop a test to measure the skull-ness of any candidate picture on a scale from 0 to 100.

Only images that show clear progress towards skull-ness are selected. All other images are discarded.

Will this effort succeed?

Almost certainly not.

Look at this sequence of images that actually generated an image of a skull.

None of the intermediate steps would have passed the skull-ness rating test.

This is why, for example, you will probably fail if you try to find a viable theory of quantum gravity by rationally combining quantum field theory and general relativity.

Physicists have been trying to do this for more than a century now with little success.

The breakthrough will most likely come from a completely unexpected direction.

If you fixate on preserving relativity’s every feature or ensuring “quantum-ness” at every step along the way, you’ll disregard the weird path that might actually lead to the correct theory of quantum gravity.

Progress requires weird tangents precisely because we don’t know where they’ll lead or why they matter.

The scientific method is supposedly this clean process for “acquiring knowledge that has been referred to while doing science since at least the 17th century.“

In the 20th century, guys like Karl Popper and Thomas Kuhn popularized now well-established models for how scientific progress happens.

According to Karl Popper, science means proposing hypotheses and then falsifying them.

Thomas Kuhn argued that scientific progress occurs through paradigm shifts, where established theories are overthrown by new ones that better explain observed phenomena.1

The resulting “Standard Model of Scientific Progress” is that we keep doing experiments until we find enough data that cannot be explained by the existing model. Then we realize it’s time for a change. Theorists propose new, falsifiable models. These get tested until we find one that explains all data, including the one the previous theory couldn’t.

A lot of the structure of modern academia is motivated by these ideas.

People are hired and papers accepted based on the idea that science progresses through a series of sensible, rational steps.

And yet, when you actually look at the history of scientific discoveries, you quickly notice that genuine breakthroughs virtually never happened like this.

Obviously Wrong Breakthroughs

Most breakthroughs were initially in conflict with observed facts. They were easy to ignore and discard because they so obviously did not fit the available data.

Take, for example, to use one of Paul Feyerabend’s favorite examples, Galileo’s proposal that the Earth is constantly moving.

This idea is obvious nonsense. Clearly, you would notice if this was true just like you notice you’re moving when you’re sitting on a moving cart.

Also, you can falsify Galileo’s theory simply by jumping into the air. If the Earth was truly moving, you wouldn’t land in the exact same spot since the Earth moved while you’re in the air.

And last but not least, we know that when the Earth does in fact move during an earthquake, the implications are dramatic and obvious.

Now, of course, Galileo’s idea is correct. But that was far from obvious when he proposed it.

It requires serious work to figure out how Galileo’s idea can be true despite all the apparent issues.

At the time of a scientific breakthrough, an incredible amount of energy has already gone into the existing incumbent theory.

There’s no way a freshly born theory can operate at even remotely the same level when it comes to explaining observed facts.

For example, when Louis de Broglie presented his framework of quantum mechanics at the Solvay conference in 1927, he was quickly shot down by guys like Wolfgang Pauli and Hans Kramers.

Pauli’s objection was based on a misleading analogy, while Kramers demanded an explanation of a complex phenomenon that de Broglie was unable to provide on the spot.

Discouraged by the criticism, de Broglie abandoned his framework.

This stalled progress for more than 20 years until David Bohm rediscovered the same framework.2

Scientific progress typically requires someone sticking to an idea even though it initially seems inconsistent with the facts and most experts think it’s stupid.

In contrast to what Popper, Kuhn, and Wikipedia suggest, scientific progress isn’t a clean rational process. It requires arrationality.

I would go as far as saying that if you adhere too strictly to the caricature version of the “scientific method” there’s a good chance you’re doing cargo cult science rather than real science.

The Anomaly Myth

Far too many researchers believe in the Standard Model of Scientific Progress.

For example, in physics, there is a widespread belief that we have to keep building bigger versions of existing experiments until we find data that so clearly invalidates our existing models that we’re forced to find new ones.

The issue is that this completely ignores the fact that it’s virtually always possible to save theories with enough creativity.

No matter what weird movements astronomers observe, you can always save the model with planet Earth in the center if you add enough epicycles.

Another story that illustrates this is when John Herschel discovered Uranus in 1781.

In the years after the discovery, several astronomers realized that Newton’s theory of gravity did not accurately describe Uranus’ motion.

But instead of abandoning Newton’s theory, they theorized that another planet, not yet discovered, needed to be added to the model to explain the anomalies.

One astronomer, Urbain Le Verrier, calculated where to find this planet, and, in 1846, this is exactly where Neptune was discovered.

A few years later, astronomers noticed that Mercury was also not quite moving as you would expect from Newton’s theory.

Once again, they didn’t throw out Newtonian gravity but instead, postulated the existence of another undiscovered planet. They called it “Vulcan.”

Several teams claimed to have discovered Vulcan over the years, but no discovery was ever generally accepted.

The puzzle was only fully resolved when Albert Einstein explained the motion of Mercury perfectly using his theory of General Relativity. No undiscovered planet Vulcan was needed.

According to the Standard Model of Scientific Progress, the anomaly in Mercury’s movement should have led to a paradigm shift. After all, the theory made predictions that did not match what was observed in experiments.

But that’s not what happened. The Mercury anomaly had nothing to do with Einstein’s discovery of General Relativity.

Physical theories are flexible frameworks that allow for an infinite number of models. So you can describe pretty much anything you observe using your current state-of-the-art theory. All you have to do is modify the model. There’s no need to throw out the theory itself.

This is also true for the current state-of-the-art theory, quantum field theory. There’s an infinite number of models you can describe using it.

Anything you observe in, say, a collider experiment you can describe using a model of quantum fields. If a future experiment finds data that cannot be fitted using the Standard Model, you can fit it by adding a sufficient number of new fields to the model.3

You can call that scientific progress, of course. But I wouldn’t call it a paradigm shift.

A paradigm shift would mean going beyond quantum field theory.

And that’s a step that will most likely not be forced on us through new data.4

Paradigm Shifts

So, in summary, the Standard Model of Scientific Progress is only suitable to describe the incremental progress happening within an established paradigm.

In physics, a new paradigm equals the introduction of a new theory. The last time a paradigm shift happened was in the 1960s when quantum field theory was invented.

Quantum field theory received harsh criticism initially. Non-sensical results were popping up left and right. It took decades before physicists understood that renormalization techniques were not simply methods of “sweeping infinities under the rug” but contain profound physical meaning.

In the years afterward, there was an avalanche of incremental progress as new models of quantum fields were proposed, falsified, and refined.

The result was the Standard Model of Particle Physics, which was finalized in the mid-1970s.

But since then, we’ve hit a ceiling. The time is ripe for another paradigm shift aka a new theory. But it’s futile to hope that it will be forced upon us by experimental data.

Instead, just like with most previous paradigm shifts before, it will require someone to propose a radically new theoretical framework that initially seems hard to reconcile with existing observations. It will face harsh criticism and dismissal from established authorities.

Someone has to be stubborn enough to pursue the idea despite widespread skepticism and initial inconsistencies.

But that of course does not mean that every new proposed theory that seems “obviously wrong” or “not even wrong” is worth pursuing further no matter what.

There are more dead ends than successful paths in science.

Eventually, new theories need to make predictions that are successfully verified through experiments.

How long should someone persevere? When should an idea be abandoned?

I wish there were any hard rules. The only thing history teaches is that there aren’t any.

That’s one key lesson: major leaps forward are not made through a clean, rational process. Instead, breakthroughs initially often seem rather irrational or dumb.

New ideas should be given more benefit of the doubt than they currently receive.

Demanding strict criteria like an “explanation of all observed phenomena” and “falsifiability” from day one is counterproductive.5

But thousands of physicists persevering for several decades without any sign of getting closer to an “explanation of all observed phenomena” and “falsifiability” is probably too much. (I’m looking at you, String Theory.)

The most important lessons, however, is that no one should wait for neat falsification of the current state-of-the-art theory or a tidy set of anomalies before proposing new theoretical frameworks. That moment will most likely never come.

The Standard Model of Scientific Progress is a fairy tale. There is no neat algorithmic process for uncovering nature's secrets.

Ultimately science is a fundamentally human endeavour.

It relies on taste and intuition. It requires a healthy dose of irrationality, the willingness to explore new ideas before data demands them, and the patience to stick with them despite initial inconsistencies - all while still insisting on experimental validation eventually to avoid endless dead ends.

Right now I’m interested in questions like Is scientific progress slowing down? and, if yes, what might be causing it?

These questions seem severely understudied.

This is puzzling because there is a widespread agreement on the importance of science.

There are more scientists and more funding for science than ever before.

And yet, little seems to be known about the science of scientific progress itself.

Is all that additional money flowing into science actually leading to more progress?

Is producing more and more PhDs really good for scientific progress? At what point do we hit diminishing returns?

What kind of research problems do professors supervising 20 students assign vs. professors supervising just 2 or 3? How does the style of supervision change and what’s the impact of that?

Can we really expect that more researchers always equals more progress? Or is there a point at which you’re becoming like the guy thinking “If two guys need two weeks to get the job done, I’ll just hire 2000 guys, and the job will be done in about 20 minutes!”

How, after all, can we quantify scientific progress and measure how it evolves over time across different fields?

And once we can measure it, how can we explain the observed patterns?

For example, as I and others have argued, there is some evidence that scientific progress is slowing down and that “papers and patents are increasingly less likely to break with the past in ways that push science and technology in new directions”.

Why could that be the case?

Are we really running out of low-hanging fruit? Is it simply getting harder to make discoveries?

Or is it possibly a shift from a pursuit of truth towards measurable scientific prestige that’s causing the slowdown? When exactly did scientists become obsessed with citations? And how is that lining up against measures of progress?

How does the observed explosion in the number of authors per paper fit into the picture? Is it because more and more specialization is needed? Or is it because co-authoring is the best way to pad your publication list? And is there any evidence that “individuals search for truth, groups search for consensus”?

What role do funding agencies play? Is there a shift towards funding more established researchers or more incremental research? Can we judge funding allocation efficiency, for example, by looking at the “ratio NIH grants funded : total NIH grants submitted for Nobelists as a measure of the quality of the NIH's judgement”?

How could we enable more risky research knowing that “evaluators systematically give lower scores to research proposals that are […] highly novel”.

Is really “every attempt to manage academia making it worse”?

Does it really make sense to demand detailed multi-year plans when there is evidence that “greatness cannot be planned”? What should we make of the fact that “the paper with the greatest impact occurs randomly in a scientist's career”?

What role does the invention of measurable scientific prestige and the widespread introduction of peer review in the 1970s play?

Are researchers getting more risk-averse? If yes, why and when did the shift happen?

And what about the optimal conditions for scientific breakthroughs at a personal level?

How did the hours researchers are allocating to different activities like teaching, research, grant writing, supervising, bureaucratic tasks change over time? Is there any evidence what the optimal allocation for scientific progress might be?

What can we learn from the conditions in which breakthrough discoveries in the past were made? Should Einstein-the-patent-clerk really only be treated as a funny story? Shouldn’t it inspire institutional changes?

Moreover, it’s definitely not phenomenology but also theoretical questions that need more attention.

How many scientists still believe in some variation of the “intellectual virus” set free by Thomas Kuhn and Karl Popper? How well do their frameworks really describe scientific progress?

Do we really have to wait until our present theories are cleanly falsified before we can hope to make further progress? (In fact, “no theory, in isolation, is falsifiable.” There are usually auxiliary assumptions that can be discarded or new features can be added like epicycles to save the current theory.)

While in recent years finally some interesting work and proposals started to emerge, it doesn’t seem nearly enough. Most questions remain unanswered.

If billions of dollars are spent on science funding every year, shouldn't at least a little bit of money be spent to try to figure out how to put those funds to better use?

AI Education: Harvard ran a study comparing physics students who work with an AI tutor against a human-led, active learning classroom and saw extremely promising results

“Not only did the AI tutor seem to help students learn more material, the students also self-reported significantly more engagement and motivation to learn when working with AI.”

AI Research: Packy McCormick shared an interesting model for what research might look like in the age of AI. Marcel Grossmann played a material role in Albert Einstein’s discovery of General Relativity by providing him with the necessary mathematical framework to make the whole theory work. AI will not take over Einstein’s role anytime soon but very well might be able to do what Grossmann did.

”In other words, the cheaper Grossmann becomes, the more valuable Einstein becomes.”

Revisiting Einstein: Sabine Hossenfelder wrote an interesting post about Einstein’s Other Theory of Everything. One idea Einstein worked on after his big breakthroughs were attempts to geometrize everything including electromagnetism and elementary particles. Together with Nathan Rosen he wrote a paper speculating if wormholes might be interpreted as elementary particles. (Modern examples of “geometric” elementary particles are solitons, sphalerons, and instantons.) Sabine is wondering if this idea “isn’t worth revisiting”.

Another interesting idea Einstein worked on later in his career is tele-parallelism. Manifolds are characterized by torsion, curvature, and non-metricity. General relativity is a theory of manifolds with non-zero curvature but zero torsion and no non-metricity. A weird feature of general relativity is that regarding all observational predictions it seems to work equally well if we consider it as a theory non-zero torsion (and zero curvature and zero non-metricity) OR non-zero non-metricity (and zero curvature and zero torsion). This seems to raise serious questions about the standard interpretation of general relativity as a model of gravity in terms of spacetime curvature. Moreover, a much richer class of theories emerges once you relax the requirements and allow, for example, as Einstein did, non-zero curvature and non-zero torsion.

Con-Artist Entertainment: Recently started listening to the The Pirate of Prague podcast and really enjoyed the first few episodes. It’s a crazy story about a czech grifter pulling off one insane scam after another.

AI News: OpenAI released Operator an AI agent that can control a web browser. Definitely a cool idea but I very much doubt there will be serious use cases anytime soon. This is one of these instances where you can produce cool demos with something that 80% works but is virtually unusable for real life use cases unless you fix the remaining 20%. Most websites have strong guardrails against automated access. The web in its current form is far too diverse in terms of technologies that are used. Most websites are quite unstable and have tons of dark patterns that regular mislead humans.

Danish Utopia: David Heinemeier Hanson shared some thoughts on why things work better in Denmark. The gist of his theory is that Denmark takes the broken window theory far more serious and rigorously punishes small antisocial behavior to prevent bigger problems. (As a German living in Denmark I very much doubt this has a meaningful impact. All examples he describes, e.g. police ticketing bicyclists, happen exactly the same way in Germany and yet the country looks very different.)

On X, he shared a second theory: immigration policy.

“Sweden and Denmark ran the world's greatest A-B test on mass immigration and the results are in.”

Whenever I'm reading papers written many decades ago, I'm immediately struck by how different they feel.

Take this introduction from one of Albert Einstein's papers I was reading yesterday published in 1928, :

"Riemannian Geometry has led to a physical description of the gravitational field in the theory of general relativity, but it did not provide concepts that can be attributed to the electromagnetic field. Therefore, theoreticians aim to find natural generalizations or extensions of Riemannian geometry that are richer in concepts, hoping to arrive at a logical construction that unifies all physical field concepts under one single leading point. Such endeavors brought me to a theory which should be communicated even without attempting any physical interpretation, because it can claim a certain interest just because of the naturality of the concepts introduced therein."

He started a follow-up paper titled New Possibility for a Unified Field Theory of Gravitation and Electricity published in the same Session Report of the Prussian Academy of Sciences 1928, as follows:

"Some days ago I explained in a short note in these reports, how by using a n-bein field a geometric theory can be constructed that is based on the notion of a Riemann-metric and distant parallelism. I left open the question if this theory could serve for describing physical phenomena. In the meantime I discovered that this theory - at least in first approximation – yields the field equations of gravitation and electromagnetism in a very simple and natural manner. Thus it seems possible that this theory will substitute the theory of general relativity in its original form."

Yes, Einstein was a masterful thinker and writer.

But pull up virtually any paper written a hundred or so years ago and you'll be surprised by just how readable it is.

The tone is unpretentious, it's clear why the work was done, and even as a physicist not specialized in the topic of the paper you can follow along.

Many papers from back then look interesting because they cover deep, fundamental problems. Also most of them describe a single idea.

The general frame for writing papers back then clearly was: This is the problem I'm wrestling with, here are some thoughts and my attempt to solve it.

There were also many papers published back then that were simply saying: Here's something interesting I noticed.

No need to make it seem like something bigger by wrapping it in a bunch of fluff.

Letters published in Nature or Physical Review Letters, for example, back then were like that.

An extreme example of this type of paper is The Ratio of Proton and Electron Masses by Friedrich Lenz, published in 1951 in Physical Review.

It's just two sentences long:

That's the whole thing.

When reading old papers, you can feel that people were just grappling to make sense of nature and oftentimes simply had fun.

Papers had rough edges, included personal opinions, and often described unfinished work.

It didn’t matter much who submitted the paper as long as the ideas seemed reasonable and were interesting.

Note, for example, how the screenshot of the paper above doesn’t mention any academic affiliation.

For most of scientific publishing’s history, “there was more journal space than there were articles to print”.

Publishing something was a way to invite feedback and get new input from fellow researchers.

Private communication between researchers was common too, of course. But publishing a paper in a journal added an element of serendipity. Someone you din’t know might send you that one missing puzzle piece.

If you look through the archives of Einstein’s writing, you can see that he regularly wrote letters to the authors of papers sharing thoughts, giving feedback, and pointing out errors in a friendly way.

As Étienne Fortier-Dubois put it, journals like Nature were more similar to Twitter than to modern research journals.

“You could write to Nature, be published within a week, and read the replies to your letter within two weeks.”

Journals like Nature were read by people wanting to stay on top of the progress made on important science questions.

Papers were meant to be read and people were actually reading them.

This is how things worked back then.

Crazy, I know.

The contrast couldn’t be any bigger if you pull up any paper published recently.

Modern papers read like they were written by a political committee.

The tone is cold, impersonal, overly careful, and professional.

There are no rough edges or opinions. All the work is finished and polished.

Even with a PhD in the field, it’s usually impossible to follow along and the motivation why the work was done is shallow at best.

The work is usually highly incremental, so you would need to read dozens of earlier papers before you could even start to grasp why the paper in front of you is important.

I very much doubt anyone is sitting down on Sunday mornings with a cup of coffee to read the latest issue of Nature.

Instead of a single atomic idea, most papers contain a multitude of claims.

For example, Dorothy Bishop, professor of Developmental Neuropsychology at Oxford University, describes in her blog:

“I recently read a paper that reported, all within the space of a single Results section about 2000 words long, (a) a genetic association analysis; (b) replications of the association analysis on five independent samples (c) a study of methylation patterns; (d) a gene expression study in mice; and (e) a gene expression study in human brains

Nature reported in 2023 that it now takes a median time of 268 days between submission and acceptance. By the time a paper gets published the researchers typically have long moved on and are thinking about completely different topics.

When someone reaches out nowadays to the author of a paper, it’s typically to tell them they forgot to cite one of their papers.

What Happened?

Let’s work backwards step by step.

This is our starting point:

• The tone in modern papers is impersonal and dry. The writing lacks style.

• Only finished, polished work is published. No work-in-progress or opinions are included.

• The work is usually incremental instead of fundamental.

• It’s impossible to casually read modern papers, even as an expert. One reason, in addition to the dense, jargon-laden writing style, is the inflation of the number of claims per paper.

We know that this isn’t simply the unchangeable nature of the genre of scientific publishing. Things used to be different a hundred years ago.

So what explains these changes?

One data point is the explosion in the number of authors per paper.

A hundred years ago, single-author papers were the norm. Nowadays, they’ve become virtually extinct.

It’s not surprising the tone in scientific papers became less personal as a result.

A second development is the introduction of peer review.

This happened much more recently than most people assume.

Nature introduced peer review only in 1973. The prestigious medical journal The Lancet started reviewing papers in 1976.

Only one of the 300 or so papers Albert Einstein published was peer-reviewed.

Unlike what most people outside of academia assume, peer review does not mean serious fact-checking. Reviewers do not replicate experiments or check calculations step by step.

Peer review’s primary function is to check a drafts’ “suitability for publication”. Whatever that means is to a large extent up to the referee to decide.

There is little direct evidence that peer review improves the quality of published papers.

But what peer review does is to make sure everyone’s main focus becomes making their draft “peer review proof”.

Peer reviewers are typically not paid. Often you’re dealing with an already overworked and underpaid postdoc.

So they’ll happily jump at the first reason they can find to quickly reject a given draft.

Bulletproofing your draft requires carefully removing anything that can be criticized.

No opinions, no works in progress allowed. (The referee will tell you to come back when the work is finished.)

You’re definitely not allowed to express any kind of confusion. (The referee will tell you to come back when you understood everything properly.)

No fun, no humor, no analogies allowed. This is serious business now. (Yes, papers do get rejected if they are “too fun”.

A smart strategy is also to cram as many claims as you can into your paper. This makes it much harder for the referee to reject the draft as “not relevant” or “not important enough”, since they have to write something about each claim.

The third development that went hand-in-hand with the other two is that researchers started caring about citation counts.

The Science Citation Index (published as a book) was launched by information scientist Eugene Garfield 1964.

This was a huge turning point since it allowed researchers to see how often scientific papers were being cited, and by whom.

Previously, hardly anyone ever thought about citations as a thing of its own since there was no way to look at them beyond the individual listings in each paper.

But once the cat was out of the bag, there was no going back.

Citations became an objective.

Garfield also invented the Journal Impact Factor to measure average citation rates.

Once people started caring about citation counts, they naturally also started thinking about what journal would help them generate a maximum number of citations:

“Suddenly where you published became immensely important. . . . Almost overnight, a new currency of prestige had been created in the scientific world.”

Savvy entrepreneurs like Ben Lewin, who founded Cell in 1974, happily put fuel to the fire.

By rejecting far more papers than they accepted, journals became selective clubs that researchers wanted to become a part of.

Older journals had to follow the trend.

The acceptance rate in Nature decreased from 35% of submitted papers in 1974, to around 12.5% in 1980 to 8% in 2024 (and most papers “are not even deemed worthy of a submission to Nature by their authors”).

Journals were no more “passive instruments to communicate science” but became active players.

The invention of scientific prestige metrics — measured by citation counts and impact factors and reinforced through editorial selection and peer review —completely transformed the dynamics of the game.

Within a few years, metrics such as the ones invented by Eugene Garfield became the primary objective.

Initially, this seemed like a good development. Having directly measurable metrics seems much fairer and effective than relying on some vague sense of credibility, authority, and importance.

Soon they were used to make funding, hiring, and promotion decisions.

But then, of course, the Cobra effect kicked in.

As it always happens, when a measure becomes a target, it ceases to be a good measure.

The resulting perverse incentives are well-documented.

So, in summary:

Papers used to be written to be read.

Now they are written to be cited and to be added to CVs.

(Yes, people do cite papers without reading them all the time.)

Every issue with modern research papers can be traced back directly to these perverse incentives.

For example, why is the number of authors per paper exploding?

Well, co-authoring is an effective way to pad your publication list:

If you team up with a colleague doing similar work and write two half-papers instead, both parties end up with their names on twice as many papers, but with no increase in workload. Find a third researcher to join in and you can get your name on three papers a year. And so on.

Anything that isn’t promising to bring in citations is no longer deemed worth doing.

It’s why no one shares works in progress or takes the time to explain their thinking properly.

This is also why every attempt to fix scientific publishing by founding a new journal that values good writing and clear explanations will fail.

Researchers don’t cite the clearest explanation but whoever published the claim first (or is the most famous).

They also don’t work on whatever they think is most interesting or important. Instead, to have any chance of accumulating a meaningful number of citations in time scales funding and hiring committees operate on, you have to work on topics everyone else is working on. This is why virtually all research published nowadays is incremental instead of creative and fundamental.

Co-authoring “peer review-proof” papers stuffed with incremental claims is how you maximize your citation count.

It’s what you have to do to win in modern academia.

And sadly, as in any game like this, the careerists are outcompeting everybody else.

So I don’t think it’s a coincidence these developments went hand in hand with the slowdown of scientific progress.

But I will fight anyone who claims this was inevitable or that the change is irreversible.

How to Fix It

There is absolutely no reason why “true seekers”, can’t tackle fundamental problems in creative ways and write about their findings, share their confusion, the roadblocks they encounter, in a personal and readable way anymore.

Incentives are an incredibly powerful force. But if you opt out from the game, they lose their power.

No one outside of academia cares about stuff like the h-index or impact factor.

Peer review, polished multi-author "blockbuster papers," selective journals, citation counting, and researchers as a class of society entirely removed from the rest, are all modern inventions.

Science progressed perfectly well for most of history before they were introduced.

Most key discoveries were made by what we would nowadays call amateur scientists and published without peer review.

Marie Curie only got an official university job after she got famous.

Einstein, of course, was a patent clerk during his annus mirabilis.

Antonie van Leeuwenhoek sold drapes to make a living and only in his pastime invented microbiology.

Thomas Bayes was a priest.

Michael Faraday only had minimal formal education.

Ada Lovelace had no official "computer science" training (it didn’t exist yet!).

Charles Darwin was a medical-school dropout and theology student.

The guy who founded genetics, Gregor Mendel, was a monk.

Norman Lockyer, the founder of Nature, was dabbling in astronomy in his spare time purely as an intellectually productive hobby. Among other things, he co-discovered and named the element helium.

George Green, who discovered a key concept at the heart of Quantum Field Theory (Green's functions), was a 19th-century miller.

George Boole, was a schoolteacher who self-studied mathematics.

The claim that ideas got harder to find and now it requires highly specialized, full-time research to make any progress is simply false.

All it takes to turn things around is that more people wake up to the fact that they too can do science.

Once enough people participate, the current system will become obsolete.

A century from now, people will look back at today's 'professional science' and laugh.

How could people get so trapped by that ultimately meaningless status game?

Until then, let them play.

And let us get back to grappling with nature, not metrics.

When I was studying physics it always seemed like all the major discoveries, especially in theoretical physics, had been made many decades ago.

The Standard Model of Particle Physics reached its final form in the mid-1970s.

The Higgs mechanism, the final theoretical pieces, came in 1964.

This would hit me every year when they announced the Nobel prize in physics.

Usually it went to experimenters confirming an old model, or for theoretical work from decades ago, or for work that didn't seem that impressive.

I remember thinking several times: Really? A Nobel Prize for that?

But maybe every generation feels that way?

Maybe there was always just a huge delay between when work was done and when it is finally recognized?

I’ve decided to finally get to the bottom of this question.

Now it’s notoriously difficult to measure scientific progress in a meaningful way.

Qualitative surveys don’t work since researchers are incentivised to hype up the progress made in their field. Otherwise, funding sources might dry up.

Published papers and citation counts are flawed metrics. Publishing and citation practices have changed so dramatically over the decades that no conclusions can be drawn.

On the other hand, the yearly awarded Nobel prizes seem like a great starting point.

There has been no inflation in Nobel prizes since no more than three people in each field get the prize each year.

Hence by looking at the year when the work was done for which the prize was awarded, we might draw conclusions about the pace of scientific progress over time.

If my gut feeling was right and prizes were nowadays primarily awarded for work done many decades ago, this should show up in the data.

We also should be able to see if this was the case in previous decades.

So I wrote a quick script that extracted the data from the official Nobel Prize website.

The chart below shows the number of prizes in physics awarded based on the decade in which the work was done.

The same trend shows up in the charts for Chemistry and Medicine.

Taken at face value these charts seem to tell us that a lot more Nobel Prize-worthy work was done in the 1950s, 1960s, 1970s, and 1980s than in the decades before or after.

Another striking pattern is that little to no Nobel Prize-worthy work seems to been done in the past three decades.

There could be, however, another simple explanation. If it always takes the Nobel Prize committee 30+ years to recognize the importance of discoveries, it would be no wonder why almost no work done in the past 30 years got a prize.

So the next thing I looked at is how the delay between when the work was done and awarded a Nobel Prize changed over time.

The chart below shows how the delay evolved over the years.

Before 1990 the average delay was 14.25 years. After 1990, the average delay is 26.04 years.

So the lack of prizes awarded for work done in, say, the 2000s is by no means normal. If the average delay was still around 15 years, we should have seen plenty of prizes awarded for work done during this period.

For example, if we imagine we had run the same analysis in 1980, this is what we would have seen:

There is, of course, a dropoff for the most recent years but a lot of the important work done in the 60s and 50s has already been recognized.

But again, there are different ways of interpreting this data.

Maybe the Nobel committee got more risk averse in recent years and this is why they started to wait longer?

Maybe the committee got dumber and fails to recognize the groundbreaking work that is done in recent years?

This could be true but I’m not aware of any plausible explanation why this would be the case.

The alternative explanation is that really fewer Nobel Prize-worthy discoveries were made in recent decades.

So the committee had to keep going back many more decades to find work that deserved the prize.

Maybe “second tier” discoveries made in the 70s and 80s are more Nobel Prize-worthy than any discoveries made in recent decades?

To figure this out we could quantify the idea that not all work that is awarded a Nobel Prize is equally important.

A few years ago, Patrick Collison and Michael Nielsen set out to do just that.

They asked scientists to competitively match discoveries against each other.

Their result? “Discoveries in physics, as judged by physicists themselves, became less important.”

In other words, the Nobel Prize committee is awarding prizes in physics for increasingly less important work.

Another sign that the Nobel Prize committee is struggling to find Nobel Prize-worthy work, is that the most recent Nobel Prize in physics was awarded for work that has nothing to do with physics at all.

The committee seems to be thinking: Instead of digging through the archives to find any work done in physics that might deserve the prize we should rather award it for truly paradigm-shifting work in an adjacent field.

Just for completeness, below is the same chart for medicine and chemistry that show the exact same trend.

So what’s the takeaway here?

It’s impossible to draw any definite conclusions from the data we looked at here. There are undeniably alternative ways to explain the observed trends.

But at least to me, the data delivers compelling evidence that scientific progress has slowed down quite dramatically in the past decades.

The reason why I’m skewing towards this explanation is that it matches my personal experience in physics.

I can’t think of a single discovery made in the past decades that the Nobel committee “overlooked”.

Many of the most interesting papers I read during my PhD were indeed written in the 1960s and 1970s.

Despite of the explosion of papers in the decades afterwards, most of them contain little of lasting value.

I also don’t hear any outcry from the research community that important recent work gets ignored by the Nobel committee.

So unlike what Betteridge’s law suggest, the most likely answer to the question in the headline “Is scientific progress slowing down?” is yes.

Now I’m aware that this is a sensitive topic.

No professors wants to hear that they contributed little in the grand scheme of things.

No one wants to admit that despite vast increases in the money spent on research little significant work is done.

If you talk about stagnation in your field you’re quickly labeled as someone who fouls their own nest since you put everyone’s funding sources at risk.

But only once we recognize the issue at hand, we can hope to solve it.

And the question why scientific progress might have slowed down is an extremely interesting and important one.

I’m highly sceptical that the correct explanation is simply that ideas are getting harder to find.

I’m not convinced that the scientific slowdown is inevitable.

But discussing this in detail is a topic for another day.

Right now Longevity influencer Bryan Johnson is speedrunning through that famous Eric Hoffer quote:

"Every great cause begins as a movement, becomes a business, and eventually degenerates into a racket."

In a sense, he's just the latest in a long lineage of charlatans making money off the promise to help people live longer, if not forever.

Like every fitness and health influencer before him, he might have started with good intentions but is slowly evolving into yet another supplement shill.

The money is just too damn good, I guess.

But that's of course all very predictable and boring.

More interesting is to talk about the fundamental problems with his approach to health and longevity.

The Shot-Gun Approach

Bryan Johnson is famously taking a "shot-gun" approach: "Let's try everything at once and see what we find."

This makes it virtually impossible to tell what's actually moving the needle.

On top of that, he's also giving little explanation for most of his choices.

If there is one paper that suggests that, for example, low doses of lithium might increase dementia risk, that seems to be good enough for him.

There are hundreds of threads on Reddit where people try to decipher why, say, he's eating macadamia nuts and strawberries but not almonds and apples.

With each supplement, with each drug, with each intervention, you're increasing the risk of unintended side effects.

It’s why “rich people often times have bad outcomes”. Doing more in a health context often backfires.

You might have done your research on the supplement vendor, but then the company gets sold to private equity and quality control goes down the drain.

Side effects might not show up immediately, but after taking some polluted supplement for a decade, they will.

So in summary, I don't think anyone is learning anything useful from Bryan Johnson's n=1 experiment.

The metrics he loves bragging about are most likely the result of just two interventions:

• Caloric restriction

• Potent anti-aging drugs (rapamycin, metformin, acarbose, 17-alpha estradiol)

These seem sufficient to explain most of the changes he's observing in his health markers.

That nutty pudding, the olive oil, or the dozens of supplements he's selling have little to do with it.

Caloric restriction (aka eating less energy than you burn) prompts the body to decrease sympathetic activity in order to conserve energy.

This shows up in measurements in the form of lowered body temperature and lowered heart rate, both changes Bryan Johnson frames as positive outcomes.

The downside, however, is that caloric restriction has severe adverse effects in the long run.

When your body goes into energy-saving mode, you - surprise surprise - have less energy. You start to feel horrible. Your body is sending you signals to change things ASAP.

Bryan Johnson seems to be mitigating this through hormone treatments (TRT) and psychopharmaceuticals, but he rarely ever talks about this.

He's already taking so much experimental stuff, why would he say no to a little Ketamine á la Elon Musk?

Potent anti-aging drugs like rapamycin basically mimic caloric restriction. There are strong indications from animal studies that they have a positive effect on lifespan.

But it's not clear why taking multiple of them at the same time while also restricting calories would have additional benefit.

If anything, the waters are muddied so much by his shot-gun approach that it's impossible to draw any conclusions.

Metric Hacking

The second problem with Bryan Johnson's approach is his obsessive focus on optimizing a set of metrics.

Yes, you can lower your heart rate and body temperature by starving yourself. But that doesn't mean it will do you any good.

Yes, you can cherry pick certain biomarkers, hack them, and then claim "I have the best biomarkers in the world. I am the healthiest person on the planet."

Buried on his website, he admits, for example, "Several heart markers including LV septal A' mitral, Aortic root diameter, LA E' latbasal and RVSP are all coming in decades older than my chrono age."

Also, he notes "severe headache symptoms causing to wake in the night."

Besides, his telomere length and most of his brain markers are around his biological age.

And that's, of course, just the stuff he's sharing publicly.

In addition, hacking biomarkers is conflating cause and effect.

I have no doubt that you can increase your nighttime erections by stimulating your penis with shockwaves.

You can make your face look younger through plastic surgery.

Your teeth do like nicer when you’re wearing veneers.

You can "de-age" your hair using potent medications like Finasteride and Minoxidil.

But I'm doubtful any of this will make you live longer.

Instead, if Bryan Johnson's other interventions were effective beyond manipulating biomarkers, would he really need any of that?

If all of his interventions really made his body 31 years younger, shouldn't this show up in all kinds of places instead of just a few selected biomarkers?

Entertainment

Bryan Johnson does a great job at deflecting any criticism that comes his way.

He managed to install an incredibly powerful frame:

"I don't get why this dude gets any hate at all. He's literally living his life as an experiment so that we can live a longer healthier life."

He's also trying to take the wind out of his critics' sails by leaning into the weirdness and scamminess of it all.

"Haha, look, I'm naming the olive oil I'm selling snake oil. I'm clearly in on the joke."

"Haha, I can't stop talking about my penis health."

Just like with his namesake Bryan "Liver King" Johnson, it might be nice entertainment.

But don't expect to learn anything useful from either of them.

Favorite Movies & Shows & Music

• Mario Barth live in Hamburg (standup comedy)

• Panickherz by Benjamin von Stuckrad-Barre (theater)

• Shantaram (TV show)

• For all Mankind (TV show)

• Slow Horses (TV show)

• Poor Things (movie)

• Vultures by Kanye West (album)

Favorite Books

• When We Cease to Understand the World by Benjamin Labatut

• What is Real? by Adam Becker

• Impro by Keith Johnstone

• The Rigor of Angels by William Egginton

• Why Greatness Cannot Be Planned by Kenneth Stanley

Favorite Restaurants

• Jungle in Singapore

• Gastromé in Aarhus, Denmark

• WAATU in Uluwatu, Bali

• Bar Vera in Pererenan, Bali

• Herbivore, Ubud, Bali

  

  

Favorite Dishes

• Char Siu at Take 31, New York City, USA

• Gemüse Kebab at Rüya in Berlin, Germany

• Beef Tartar at AuGust, Zurich, Switzerland

• Wagyu Ramen at Fukagawa Ramen, Berlin, Germany

• Bone Marrow at Tanau in Canggu, Bali

• Lunch Ramen at Sensorium, Canggu, Bali

• Duck Laab at Jungle, Singapore

• Spicy Chicken Ramen at Micho Ramen, Vienna, Austria

• Königsberger Klopse (home-cooked)

• Smoked trout with sweet potato rösti and melon salad (home-cooked)

Favorite Bars

• The Bvlgari Bar in Bali

• Vault in Berlin, Germany

• The Bohemian in Hamburg, Germany

Favorite Activities

• Visiting the house of Halldor Laxness near Reykjavík, Iceland

• Ice bathing in Nuuk, Greenland

• Cruise with my dad from New York via Canada and Greenland to Iceland

• Attending live recording of Late Night Berlin in Berlin, Germany

• Puppy yoga in Canggu, Bali

• Jeep tour in Bali

• Jeep tour in Iceland

• Sunset yoga at Wrong Gym, Perenanan, Bali

• Watching the sunset in Perenanan, Bali

• Watching the sunset in Zadar, Croatia

• Learning improv comedy

How can a single human make so many breakthrough discoveries?

And how come, despite our supercomputers, global research networks, and instant access to virtually all human knowledge, we haven't seen another Einstein?

This is a question I’ve been pondering for years.

I've identified five puzzle pieces that, taken together, start to hint at a convincing answer.

Let's talk about them one by one.

Education

Einstein received aristocratic tutoring.

Max Talmud introduced the young 12-year-old Albert to geometry. His uncle taught him algebra.

This type of path- and goalless tutoring that plants seeds of curiosity and teaches intellectual agency through osmosis has become extinct.

Tutoring nowadays is always focused on improving grades in specific tests.

Entourage

Before taking up his post at the patent office in Bern, Einstein offered private lessons in mathematics and physics to make a living.

One of the students that replied to his newsletter ad, Maurice Solovine, quickly became a good friend.

The two began to meet regularly to discuss physics and philosophy. Soon a former neighbor of Einstein also joined the discussions regularly.

They started to call their gatherings Akadamie Olympia. Guests sometimes joined.

They discussed their own works in progress and books like Karl Pearson's The Grammar of Science and Henri Poincaré's La Science et l'Hypothèse (Science and Hypothesis), John Stuart Mill's A System of Logic, David Hume's Treatise of Human Nature, Baruch Spinoza's Ethics, and Miguel de Cervantes' Don Quixote.

These gatherings played a significant role in Einstein's intellectual development leading straight to his annus mirabilis.

Students nowadays are far too busy with structured coursework for goalless intellectual pursuits like this.

Deep intellectual curiosity is also far rarer thanks to the modern school system and all the distractions that constantly compete for our attention.

As a result, there is no critical mass to form their own Akademia Olympia in most people’s personal networks.

Exposure

Einstein was exposed to the right problems at the right time.

One of the books they discussed at Akademia Olympia, Henri Poincaré's La Science et l'Hypothèse, lays out precisely the problems Einstein solved during his annus mirabilis.

Maurice Solovine reported that Poincaré's book kept them "breathless for weeks on end".

What is today's equivalent to Henri Poincaré's La Science et l'Hypothèse?

I’m not sure there is one.

Science has become far more specialized.

There are few researchers that have a full grasp of their field and its problems.

Book’s à la La Science et l’Hypothèse are not valued in today’s academic system.

And most researchers are far too busy writing grant applications and churning out incremental papers anyway.

Exploration

In the years leading up to his annus mirabilis, Einstein had the freedom to explore instead of being constrained by definable objectives. (Later in his life he lost this when he became fixated on the idea of a unified field theory.)

There is no way to get funding for open exploration in the current academic system.

Despite there being more professional researchers than ever, everyone is too busy carrying incremental research.

It’s publish or perish. To publish, you need results. To get results reliably, you need to pursue safe, incremental research with predictable outcomes.

Even though many people are aware that their research is “almost certainly bullshit”, no one is able to escape the chains of the academic system. In its present form, it only rewards hill climbers but not valley crossers.

The best way to win a grant is to write proposals that are perfect compromises; equivalents of the color purple in fashion.

Good enough to satisfy everyone, sure not to offend anyone, but ultimately mediocre, diluted, toothless, and forgettable.

As Joel Lehman and Kenneth Stanley convincingly argue in their book:

“Seeking consensus prevents traveling down interesting stepping stones because people don’t agree on what the most interesting stepping stones are. And resolving this kind of disagreement often leads to a compromise between opposing stepping stones. […] So when consensus is sought in exploration, the result is a generic washout effect. Instead of allowing each person to discover their own chains of stepping stones, the system squashes a diversity of opinions into a generic average. Perhaps then it would make sense sometimes to reward maximal disagreement instead of agreement. It’s possible that anti-consensus may be more interesting than bland agreement. After all, attracting a unanimous vote in science could be a sign of nothing more than echoing the status quo. If you’re doing whatever is hot and parrot the right buzzwords, you might be able to attract wide support. On the other hand, an interesting idea is likely to split votes. At the border between our present knowledge and the unknown are questions whose answers remain uncertain. That’s why the opinions of experts should diverge in such uncharted territory. It’s in this wild borderland between the known and the unknown that we should want our greatest minds probing, rather than within the comfortable vacation-spot of maximal consensus. If experts all agree that an idea is terrible, as in poor, poor, poor, poor, then there’s no evidence that it’s worth pursuing. But when experts radically disagree with each other, something interesting is happening.”

Ecosystem

Einsteins Annus Mirabilis famously happened outside the academic system.

But instead of taking any lessons from this, modern academia has become even more rigid and institutionalized.

As a result of the Second World War, the number of PhDs in physics exploded.

The scientific community is very different in the era of Big Science.

To quote Samuel Goldsmit:

“A quarter of a century ago, we could exchange ideas in Bohr’s study with no government secrets, weapons programs, or spy cases to bother us. … None of us were distracted by offers to become college presidents or big wheels in industry, and governments didn’t give a hoot about physicists. There was no trying to elbow one’s way to power, for the simple reason that there wasn’t any place to exercise power. No huge laboratories, no military projects. … We all felt that we belonged to a sort of lodge, with a worldwide membership of only four hundred or so, and everyone knew everyone else well—or at least knew what everyone else was doing. Now four times that number will turn up for a meeting of just American physicists, and most of them will be strangers to each other.”

The reason why Einstein was able to make scientific contributions outside the system was because the scientific community was small enough.

When Einstein, with no scientific affiliation at the time, submitted his groundbreaking papers, the physics community was small enough to take notice and take it seriously.

The small, tight-knit community meant ideas could flow between insiders and outsiders.

There was no need for peer review.

Only one out of Einstein’s 300 papers was peer reviewed.

Nature introduced external pre-publication review only in 1973.

Editors decided what got published, often only relying on personal connections and informal recommendations.

In the pre-WWII era, editors actively solicited articles from personal connections or filled in gaps in journals themselves. Editors were happy to receive article submissions.

Today? It’s the exact opposite.

With hundreds of researchers in every field fighting for a tiny number of secure positions, always ranked against each other based on their publication records and citation counts, it’s no wonder journals are flooded with submissions.

The current situation is summarized by the following joke in David Lindley’s book A Different Universe:

“The Physical Review is now so voluminous that stacking up successive issues would generate a surface traveling faster than the speed of light-although without violating relativity because the Physical Review contains no information.”

Most professors barely know their students, let alone introduce them to their colleagues.

So a paper by a until-then mediocre PhD with no academic affiliation would most likely be ignored or rejected outright in today's system.

Moreover, many historic paradigm-shifting papers like Turing's founding paper for computer science barely deserve that name by modern standards.

But that is saying more about our modern standards than about the quality of those papers.

In summary, the absence of a "new Einstein" isn't due to a lack of brilliant minds or scientific potential, but rather to the systematic dismantling of the conditions that made Einstein possible.

Today's rigid educational system, the scarcity of deep intellectual communities, the hyperspecialization of science, the pressure for incremental progress, and the bureaucratization of academia have created an environment that would likely have stifled even Einstein himself.

Until we can recreate the conditions that fostered revolutionary thinking in the past, we will continue to see diminishing returns in scientific breakthroughs.

How come Einstein accomplished so much in his early years and failed to produce anything meaningful in his later years?

Did his cognitive abilities simply decline as he got older? Maybe.

Was the frictionless environment at the Institute for Advanced Studies actually harmful? Possibly.

But I now think the main factor is something else: Einstein fell prey to the grand objective fallacy.

It roughly goes like this: Grand things are accomplished by visionaries who set their sights on a clear objective and relentlessly keep going until they get there.

It's a narrative the human brain loves.

It's like a comforting blanket in an otherwise overwhelmingly confusing world.

The only problem? It's completely fake.

In hindsight, it's always possible to connect the dots in a way that fits the grand objective story arc.

But that doesn't mean this is really what happened.

The real story is often far too confusing, weird, and frankly boring.

Big things are usually accomplished by people following their hunches and intuitions with no clear plan or objective in mind.

People fixated on some grand objective tend to get stuck and never accomplish something meaningful.

That's precisely what happened to Einstein in his later years.

His grand objective was to develop a unified field theory. That never worked out.

Sure, if you aim high it's not too surprising when you fail.

But the real tragedy is that none of the ideas he developed while working on his unified field theory had or have any relevance to other researchers.

Einstein's approach earlier in his career was way different.

He didn't have a grand masterplan to revolutionize our understanding of energy and matter or to overthrow classical mechanics or Galilean relativity.

Instead, he was just following his hunches and intuitions, solving problems that were right in front of him (quite literally in the form of Henri Poincaré's book Science and Hypothesis).

There are experiments backing up this idea.

Researchers training robots tested two different approaches:

• Train using objectives like "get out of the maze" or "walk".

• Train using novelty search where the robots simply try to do something different than they had done in the past.

Interestingly, novelty search outperforms traditional objective-based algorithms in most scenarios.

Robots learn faster and more reliably to navigate out of a maze by always trying something new instead of focusing on the objective "get out of the maze".

This works because after crashing into enough walls, crashing into a wall stops being novel. So the only way to do something novel is to not crash into walls.

In contrast, robots focused on getting out of the maze often get stuck.

A deeper force at play here is that objective-based algorithms provide an ordering from "good" to "bad".

With a clearly defined objective you can directly assess any action using it.

The issue with this approach is that the stepping stones that actually lead to the objective are often unpredictable.

Just like Einstein with his ambitious vision of a unified field theory, robots get stuck in cul-de-sacs because the steps leading there look promising when comparing them to the objective.

In contrast, novelty search, provides an ordering from simple to complex.

Once all simple behaviors are exhausted the only ways to behave that offer something novel are complex.

Novelty search can't of course guarantee that you will reach a specific objective.

But it usually leads to interesting outcomes. That's a direct result of the implicit ordering from simple to complex.

Objective-based approaches, on the other hand, can't guarantee success either. But they typically don't lead to interesting results along the way.

This also matches my personal experience.

Every time I set out to do something grand I failed.

Everyone I know who set out to do something grand didn't.

And again, the real tragedy is that nothing meaningful came out of these periods as a byproduct.

In contrast, everything meaningful I created was the result of open exploration without a plan or objective.

For example, my first book, Physics from Symmetry, was not the result of me trying to write a book.

I was just taking notes for myself, trying to figure out how far I can get in deriving the theories of modern physics just using symmetries as my starting point.

Only after many months when I talked to a friend about the project he mentioned "so this is like a book, you should publish it".

That's when I realized "He's right!". I had indeed written a book without realizing what I was doing.

I always made more money and had more people reaching out to me to say thanks whenever I wasn't trying to make money or help people.

The lesson that novelty search trumps objective-based approaches is an incredibly hard lesson to execute on.

Virtually every biography reinforces the myth of the grand masterplan, the big vision.

So we feel like if we also want to accomplish something big, we should follow a grand vision and develop a masterplan.

You can't just follow your hunches and hope that something good comes out of it.

That's just not how things work.

Except it is.

As soon as you let anything but curiosity be the driver and rudder you are on the path to failure.

But for how many people is curiosity the sole driver?

Few.

Which is why few meaningful things get done.

Which is why letting yourself be guided by curiosity feels so weird.

For most people objectives like money, status, doing something that sounds cool, are the driver and rudder.

And no human is totally immune to these mimetic forces.

Even, for example, most researchers are driven by other factors like status above all else.

You can't get funding for open, curiosity-driven exploration.

Which means there is no place for curiosity-driven researchers in today's academic system.

Which is why scientific progress is stagnant in so many fields.

At one end of the spectrum you have academics carrying out incremental research purely driven by short-term objectives.

At the other end of the spectrum you have crackpots driven by ambitious objectives never producing anything relevant.

You have startup founders with big visions failing to change the world and millions of people solving incremental problems for a regular salary.

There's simply no one "chasing hunches and interesting problems without narrow material and objective constraint”.

Yes, this is all a bit sad to think about.

But it also means that if you're able to fully embrace an open-minded, objective-free approach you have an insane competitive advantage.

There's no competition because everyone else is getting stuck in local maxima.

The big secret is that a purely curiosity-driven approach works.

You might not get rich or famous or make a ground-breaking discovering.

But the odds are good that something interesting will come out of it.

To me this feels like forbidden knowledge.

The whole school system is designed to brainwash every member of society to always have clear objectives.

You're not supposed to wake up each day and fly by your own creative compass.

You should have an objective like making enough money to buy a nice house or do something good for humanity.

Goals have an "irreproachable and unimpeachable status".

At any time you should have a good answer to the question "What are you doing?".

"Just exploring" is not an acceptable answer unless you're 23 and on a backpacking trip through Europe.

The key is to realize that drifting through life and exploration while looking similar from the outside are actually polar opposites.

Drifting is passive and leads to a narrowing of perspective while exploration is, well, active and widens it.

A stable society, of course, needs processes driven by clear short-term objectives.

Short term objectives are important when the path from A to B is clear.

But paradigm shifts, dents in the universe, those genuine leaps forward come from poking around, exploring, and following hunches, not grand visions or masterplans.

Einstein lost track of that in his later years.

So did you.

So did I many times.

And that's why I wrote this.

Really as a reminder to myself.

It's time to go explore again.