Why does independent research from people without formal academic qualifications generally turn out to be a complete waste of time?

Question

I personally relate with people (wannabe physicists) who want to do something BIG in Physics and Maths, but don't have a high-level education (PhD) suited for it. Reasons could be a lack of jobs in pure science and the amount of time a PhD or postdoc takes.

When such people who truly love exploring and researching somehow end up doing something totally different as a job, they try to stick to studying science as their hobby. Many of these people later write research papers which they have produced themselves, targeting the big question-marks we have in science and try to get a review out of real physicist by sending them their work. But most of them (99%) are straight up wrong and miscalculated.

Why? How is the learning process for these people so different than the ones doing a PhD that their work is not even worth a real physicist's time? I mean they (wannabe physicists) must have also read tons of books for their research, they must have thought a lot, they must have gone through hundreds of research papers themselves, the only thing they might truly be lacking is seniors in the field to guide them; but I am sure many people doing PhDs also don't get that much guidance. So what might set them apart so drastically?

Answer 1

I think a lot of the other answers touch on these things, but I thought I'd make it explicit:

• Most claims by professionals to have solved the Big Questions are also wrong. Often as a professional, you wouldn't see another professional cold emailing you with "evidence" for their solution, because someone local will already have pointed out the mistake. This will often be a supervisor or a mentor. The reason that people who no longer have a supervisor or mentor rarely make these mistakes is...

• Most established professional researchers don't try to solve the Big Questions. Most of them have long since given up on such things as insoluble. Even if they haven't, they have to work on things that can secure research funding, and many of the outstanding Big Questions are too risky for research funders to fund. At best they work on small things that are tangentially related to a Big Question and might help others move forward in the future. In this way, most Big Questions are not solved in one go by a single genius but are chipped away at over decades or even centuries.

Most amateurs have not had the important but disillusioning experience of realising that they themselves are not going to revolutionise the world, and they are at best just one cog in a long and on-going machine of incremental progress. Nor have they had someone to guide them through this realisation and help them come to terms with it and decide if they can live with that.

In addition, they do not talk about ideas over coffee every day, have their ideas shot down in departmental seminars, have their grants critiqued by reviewers etc. on a regular basis, and have sharpened and honed their arguements as a result.

It's worth noting that having your work shot down, dismissed, or otherwise rejected is also the default experience of any professional researcher proposing something.

Answer 2

I'll share an analogy. In early 2023 I started ten-pin bowling regularly as a way to get some exercise. I worked out multiple times per week, practiced at home, watched lesson and competition videos, played in a league, etc., and saw my scores go generally upwards. I did get injured once or twice and had to take some weeks off to recover.

After about a year, I decided to see a coach. When we first met, I took a few practice shots, and he said, "I'm not sure we can work on anything useful today because the finger hole inserts on your ball are way too loose. You need to get those replaced ASAP." (I put some tape on my fingers and we did work on other stuff for an hour.)

A day later I went to a shop and got the ball fixed, and the whole feel and sensation of throwing the ball completely changed; it was immensely more snug and changed everything about my grip and release (allowing me to focus on other issues). Then I had to take a few months to re-learn how to throw it before seeing my coach a second time. In that time I became the best bowler in my league and broke all the high-score records for the season.

Now, my point is, that was just one lesson with an expert trainer in the field (and in fact just a couple minutes into that lesson). He could immediately pick up on a grip and feel issue which no amount of documentation, articles, or training videos could identify. If I'd seen him up front I surely would have saved at least 6 months of practicing and (I think) two injuries which set me back.

If we extrapolate that one data point across, say, meeting with an advisor just once a month for 6 years of a PhD, then the effective time advantage would be something like 36 years, i.e., effectively an entire added working career (and maybe a dozen fewer self-inflicted injuries). If the meetings are weekly and similarly-productive, then the advantage could be estimated at 144 years, well beyond anyone's working lifetime.

Answer 3

You underestimate the impact of an advisor. Even assuming that these wannabe physicists really have read tons of books and gone through hundreds of research papers (I suspect most of them have not), reading is not research. Reading can get you the background, but you don't get a PhD by reading. You need to do research, and research is fundamentally different from reading.

When you do research, a lot of the time you will hit the "this doesn't work, I have no idea what to do next" wall. Surmounting this wall is very difficult without an advisor. The advisor can help by suggesting new things to try, identifying unproductive lines, recommending papers, and more. They've been around a lot longer, and they have a much better idea what to attempt. You'll know this firsthand if you've ever tried to teach elementary physics to a younger student - a lot of the time what's extremely obvious to you is not obvious at all to the student, and when the student asks "how do you know this is the correct way to approach this question?" the only real answer you can give is "because I've seen similar questions before".

Furthermore, a lot of the time in research, the advisor will also have no idea what to do next. That's why Einstein once said "If we knew what it was we were doing, it would not be called research, would it?"

It's in theory possible for academically unqualified wannabe physicists to make meaningful contributions to Big Question research, just like it is in theory possible for a student to master elementary physics from a textbook alone, but it is a lot harder, to the point where most people simply cannot or will not put in the required effort. Remember the PhD is already ~5 years of full-time work. Wannabe physicists working alone will surely take significantly more time - and if the wannabe physicist is not able to get a PhD because of (as you put it) "the amount of time a PhD or postdoc takes", how are they ever going to put in the time required to get a PhD without an advisor?

That ultimately is the underlying reason: making progress takes work, and most wannabe physicists have not put in the required amount of work.

Edit: The day after I wrote this answer, I read the following article on Quanta about the proof that BB(5) = 47,176,870. The proof resulted from a collaboration of enthusiasts, one of whom (Maja Kądziołka) didn't even finish undergraduate studies. So yes, amateurs can make meaningful contributions. But you can also see that they put in a huge amount of effort (at one point working through the night), and moreover, collaborated with people who did have formal training and can therefore serve as impromptu advisors. It can be done, but it is hard.

Answer 4

Peter Flom gave a good answer but I want to address some other aspects. Most of this answer will focus on pure math, but aspects will apply to other STEM fields. (It is also worth noting that a lot of amateurs do good work, or do fun work in things like recreational math and we don't notice them quietly being productive.)

One: there are certain classes of mistakes that when you get a regular education in a topic get pointed out to you, as well as theorems which show that a particularly approach to something simply cannot work. Here are three examples in pure math which amateurs seem to miss: First, the relativization barrier and natural proofs barriers showing that a lot of strategies for showing that P != NP cannot work(relativization also blocks a lot of strategies for showing that P=NP). Second, the orbit of -1 shows that a lot of naive modular arithmetic approaches to the Collatz conjecture must fail. Third, the existence of Descartes number shows that a lot of strategies for proving that no odd perfect numbers exist, while not actually using the genuine primality of the prime factors must fail.

Edit: I'm including here at the suggestion of the comment below a bit more about how these roughly work: If you don't care about this feel free to scroll down past the next few spoilered paragraphs and skip to the paragraph which starts "Curiously" and you'll get back to the general points.

For the first example, whether P=NP, the question is roughly speaking whether the set of problems which are easy to tell what the answer is is the same as the set of problems where given an answer one can quickly check this. The guess is that this is no. Roughly speaking, there should be classes of puzzles where finding the solutions are hard but checking a solution is easy. For example, solving a jigsaw puzzle feels much harder than checking that a solved puzzle is solved. Similarly, solving a Sudoku is tough, but verifying a solved Sudoku is easy. Proving this rigorously though is apparently beyond current math, but P roughly corresponds to the set of puzzles which are easy and NP corresponds to the set of puzzles which you can check solutions easily. So the conjecture that P is not equal to NP is the conjecture that there are classes of problems where it really is tough to find solutions, but checking a solution given to you is easy.

The difficulty mentioned above is that you can imagine what we call an "Oracle" which is a special machine which can answer some very tough set of questions for you, and you can then imagine puzzles where one is allowed to solve things with the Oracle as an assistant, and depending on your Oracle choice, you get different versions of P and NP. It turns out that depending on your choice of Oracle, you can get your versions of P and NP to equal each other or not be equal. But and here's key point, most of the obvious techniques to try to resolve a question like this will not look any different if there is also an Oracle attached. So that means those techniques cannot resolve this problem by themselves, since if they did, it would tell us that that occurred regardless of our Oracle choice, which is not the case.

The Collatz conjecture (sometimes called the 3n+1 problem) is one of the most famous open problems, and I should warn anyone that if you have not seen it, it is a genuinely dangerous thing to know about. You may try to spend a lot of time thinking about it once you hear about it! You've been warned. Ok: So here's the idea. We're going to start with a natural number, and when it is even, we'll divide by 2, and when it is odd, we'll multiply by 3 and then add 1. We'll keep repeating this but we'll stop if we hit 1. For example, let's say we start with 22 22 is even so we divide by 2 to get 11. 11 is odd so we multiply by 3 and add 1 to get 34. 34 is even so we divide by 2. So we get a sequence. If we write this out for 22 we get 22, 11, 34, 17, 52, 26, 13, 40, 20, 10, 5, 16, 8, 4, 2, 1. The conjecture is that no matter what number we start with, we'll end up eventually hitting 1 and stopping. This seems really simple but we cannot prove it!

Now, one way of thinking about numbers that is helpful is what is called modular arithmetic. You've seen a version of this already but might not realize it. When you tell time, you use it. For example, if it is 10 o'clock, and you want to know what time it will be in 4 hours, you add 4, get 14, and then subtract 12 to conclude it will be 2 PM. So all you cared about was the remainder when you divide by 12. If you are in a country where you use 24 hour times, you'll care the same about the remainder when you divide by 24. And you do something similar with days of the week. If today is Friday, and you want to know what day it will be in 10 days, you don't need to count out 10 days. Instead, you count out 3 days, because 7 of them will loop. Modular arithmetic is looking at the remainder when you divide by a specific number this way, and is one of the most fundamental techniques of number theory. If you've seen puzzles that involve looking at just the 1s digit of a number, you are really doing modular arithmetic with respect to the number 10. (We would say the first example is mod 12, the days of the week are mod 7, the digits are mod 10, and so on).

One might hope that all one needs to do is something using some specific choice of mod to understand the Collatz conjecture. And for some very similar problems you can do that. But for the Collatz conjecture, it turns out that you cannot. Here is one way to see the barrier with a specific example; we'll look at mod 5. Suppose that we have a number n which leaves a remainder of 4 when we divide by 5, (say 9) and suppose we apply the Collatz function to it. So we multiply by 3 and add +1. Then we have that 3n+1 is leaves a remainder of 3 when you divide by 5. But then if we divide by 2, we are left with a number that is 4 mod 5 again. So we cannot use mod 5 to conclude much because we might get stuck in an indefinite sequence of numbers like this and mod 5 won't be able to notice. Something similar happens for say numbers which leave a remainder of 9 when you divide by 10, or numbers which are 55 when you divide by 56. In general, for any mod m, m-1 will act in a similar way. So this means that you cannot solve Collatz by just thinking about modular arithmetic.

Our third example: A famous old problem is whether there are any odd perfect numbers. A number is said to be perfect if when you add up all the factors of a number which are less than the number you get the number itself. For example, the factors of 6 which are less than 6 are 1, 2, and 3, and 1+2+3=6. So 6 is perfect. (In contrast, the factors of 8 which are less than 8 are 1, 2, and 4, and 1+2+4=7, so 8 is not perfect. (Note: Some people use factor to include negative factors so -2 would be a factor of 8. For simplicity I'm using factor here to mean positive factors.) The first few perfect numbers are 6, 28, 496, 8128... and they have been studied since the ancient Greeks. All known perfect numbers are even. Two of the oldest unsolved problems in all of math are are there infinitely many perfect numbers which are even, and are there any perfect numbers which are odd? Now, it turns out that for many purposes, it is easier to instead of looking at the sum of the factors of a number which are less than a number, but to include all of the factors (that is include the number itself). This leads to what is called the sigma function, denoted not too surprisingly with the Greek letter sigma, 𝜎(n). For example, 𝜎(6)=1+2+3+6=12. Note that using this function, n being perfect is equivalent to 𝜎(n)=2n. 𝜎 has a particular nice formula in terms of its prime factors. Here's an example of how it works: Take 60. It turns out that 𝜎(60)=168. Also 60 = 4 times 3 times 5, and 𝜎(4)𝜎(3)𝜎(5)=(1+2+4)(1+3)(1+5)=168. This is not a coincidence! This works in general as long as one keeps powers of different primes. Note they really have to be different primes. It is not true for example that 𝜎(8)=𝜎(2)𝜎(4).

Now, Descartes noticed that the number D=198585576189 had a very interesting property. D= (3^2)(7^2)(11^2)(13^2)(22021). So if one takes 𝜎(D) one has 𝜎(D)=(3^2)𝜎(7^2)𝜎(11^2)𝜎(13^2)𝜎(22021)= (3^2+3+1)(7^2+7+1)(11^2+11+1)(13^2+13+1)(22021+1)=2D, so D is an odd perfect number! But there's a problem which Descartes was aware of: we've calculated 𝜎(22021) wrong by assuming 22021 is prime. In fact, 22021= 19^2 times 61. Bummer. But here's the annoying thing: the calculation above almost works, except for this little problem. And a lot of proof strategies which would prove no odd perfect numbers exist would also show that no numbers which are perfect if we "forget" that a factor like 22021 is not actually prime should be able to exist either.

Curiously, all of these are also things which one sees occasional professionals do also, but often people who are from slightly adjacent areas who try to move into one of these problems.

There's also a lot of rules about how to approach things that will make one less likely to make mistakes that amateurs don't pick up on. For example, proofs by contradiction are known to be highly perilous because an algebraic mistake can simply lead to an apparent contradiction. Thus, professionals try to prove as much as they can directly in a series of lemmas, and only reserve contradictions when they put those together. This also has the advantage that one can then often check those lemmas against concrete examples. One sees similar issues in other areas; physicists for example know they need to be really careful when doing a coordinate transformation in Special Relativity.

There is an unfortunate additional issue which is ego. A lot of the amateurs have massive egos and think they are therefore the brilliant people who are going to solve major things. In fact, a lot of people have that level of ego in undergrad or early grad school. But the academic process manages to disabuse them of that to some extent, while also getting them to calibrate what problems they can work on. Amateurs have not gone through that process.

Another aspect is that often the amateurs aren't aware of the minor problems, so they spend their time beating their heads against the walls on the major or famous ones since those are the only ones they know about. For example, there is an excellent book, Richard Guy's "Unsolved Problems in Number Theory" which lists a few hundred open problems with references. About 3% of those are somewhat famous problems (Collatz, Goldbach's conjecture, twin prime conjecture, odd perfect numbers, etc.), but amateurs are often not looking at books like that. So they are not even aware of all these other worthwhile problems which have had many fewer people think about and therefore are much more likely to have low hanging fruit.

Answer 5

Expanding on the excellent idea described in @DanielRCollins's answer, I would like to propose that the principle that the story in that answer illustrates so well has to do with the difference between formal and informal knowledge.

As an aspiring independent researcher, I'll assume you would have access to the entire body of formal knowledge of physics (or whatever discipline you have decided to research): you can walk into a university library near your house and look at books there, and you can download any academic textbook or paper you're interested in; maybe not entirely legally or for free, but let's just assume you have that kind of access.

It seems to me that built into your question is the implicit premise that since independent researchers have access to the same formal knowledge that researchers in academia have, they ought to have the same ability or at least a somewhat similar ability to do research successfully.

But what this fails to take into account is that as an independent researcher, what you don't have access to is the still quite large, and still critically important, body of informal knowledge of physics and physics research. This is a set of facts and skills that's so tenuous and elusive that most people -- even most physics researchers -- barely know it exists. It is not codified or written down anywhere (except for occasional snippets of wisdom you might learn from MathOverflow, physics.stackexchange, or blogs of influential people like Terry Tao). And yet, this knowledge consists of numerous bits of information that are extremely important to acquire in order to successfully do research.

Some examples of informal knowledge are:

• The knowledge of many open problems in the particular area you're researching, their approximate level of difficulty, and what partial progress has been done on them.

• Familiarity with various kinds of sanity checks you can run on an argument relevant to a particular subject in order to test your knowledge of an idea you have or to test your understanding of a standard theorem or calculation from the literature. (These sorts of sanity checks can be very area-specific; for example, in probability it is standard to check if the answer to a calculation of a probability is between 0 and 1. In physics you might check if the energy you calculated is positive or negative. Algebraists, topologists, number theorists, etc all have their own bags of tricks and sanity checks they apply to their ideas as a matter of routine, often subconsciously.)

• The ability to read critically through a text you or someone else wrote and spot errors.

• The ability to pursue research ideas in a systematic fashion without getting bogged down in technical notation and without falling into all kinds of traps and dead ends that are obvious to people trained in the art of research. (In particular, the ability to protect yourself against self-delusion and wishful thinking, which are common pitfalls that afflict independent researchers.)

• Etc

Summary: academia can be thought of as a distributed system of storage for a large body of knowledge that researchers tap into when they do research: the informal body of knowledge about how to do research successfully. Access to this body of knowledge is provided through a kind of search engine called "meeting with your advisor" (and/or meeting with peers and colleagues, taking a graduate class, or otherwise interfacing with live human domain experts). Independent researchers have almost no access to this knowledge base, and as a result are at an extreme disadvantage when it comes to doing research successfully.

And this principle is of course true for many other areas of human activity, as illustrated by Daniel Collins's bowling anecdote. It is similarly difficult for anyone to become self-taught to a professional level at various other things, e.g., to become a concert pianist without ever taking a music lesson, even if you have access to the entire body of formal knowledge of the domain you are trying to master.

Answer 6

Academia is a constant feedback loop of rejection and criticism. Questions from your committee and advisor during PhD. Rejection or major revision requests for papers. Rejected grant proposals. Tough questions after a conference presentation or lecture. This provides constant opportunities for refinement and exclusion of bad ideas. Second, and not to make it all sound negative, are all the positive, and reinforcing interactions of publishing, interaction with peers in your group, department, and within the broader field.

All of these mean that ideas are constantly refined. If you work in too much of a bubble without real and constant feedback, you start to believe your own nonsense.

Answer 7

Ph.D. Engineer here, former professor. I have had several experiences with 'civilians' who thought they were making a significant contribution.

My experience may be different from Physics / Math. In Engineering, the majority of people have a BS as their terminal degree. They go to industry, they have the opportunity to work with highly experienced engineers, spend a career solving hard problems, learn continuously, and are able to make contributions at a high level. As others have pointed out, progress is incremental, not revolutionary.

I have been approached by several crackpots. These experiences followed a relatively tight pattern -- there could be a description in DSM.

None of them were well studied or read. None of them had any college level education. Instead, they operated on their intuition -- what they 'knew' to be true -- and some research from faulty non-rigorous sources.

They were superficially aware of their lack in background, but were entirely unaware of the consequences of that lack of background. Often, they reached out to a professor saying something like "I know this will work, I just need someone to run the numbers for me".

They refused to acknowledge any argument that refuted their idea. Even the most simple engineering or mathematical principles could not shake them from their truths.

One gentleman was convinced that placing magnets in a circle could create perpetual motion because another magnet would be pulled forward to the next one as it went around -- ignoring that the previous magnet would retard it once it was past...

Formal education and most academic pursuits start at the bottom and build from there. Each step is taken in a formal and rigorous way that ensures the next level is sound and secure. As it turns out, there is value in that process and there are problems when you try to skip steps.

I will forever remember one direct quote from my first crackpot...

"I don't understand why airplanes are so expensive, so mine won't be."

If only it worked that way.

Answer 8

There are several reasons:

First, in general, these people don't know what they are doing; they haven't had the proper training; they haven't been fully exposed to the literature; they don't know the methods; and so on. This isn't always true, but it often is. And it applies to all research, not just "big question" research.

Second, "big questions" have received and continue to receive a lot of attention. That's part of what makes them "big". While it's not impossible for an untrained researcher to come up with a solution, it's unlikely.

Third, big questions tend to draw cranks and cuckoos. Again, not always but often. People who have a perpetual motion machine, or have shown that pi is rational, or whatever. No. They haven't. But they are very, very, sure that they have. Slightly more seriously, tons of people thought they had proven Fermat's Last Theorem before Wiles actually did it. (Very likely, Fermat was among these deluded people).

Serious amateur researchers will concentrate on much smaller questions, or ones that not many are interested in. There, they are much more likely to make a real contribution.

Answer 9

The difference seems to be the guidance they do receive. So the question now becomes why does it feel like "many people doing Phds also dont get that much guidance", while they still get so much that it makes such a big difference. A couple of ideas:

1. A little guidance over a long period (3, 4, or more years) still adds up to a lot guidance.
2. The guidance may be little, but is focused on the right topics. An amateur could spent a lot of time, but that does not do them any good if they get lost in a lot of rabbit holes.
3. The guidance may only feel like not much, especially since it is often aimed at "nudging" the student in the right direction so they can "discover" the skills and tricks that need to be discovered.

Answer 10

Here's a universal algorithm which, in my experience, allows me to solve every problem in mathematics.

1. Think about the problem for a long time and come up with a lot of relevant computations.
2. Make a typo or a subtle error in one of the formulas which leads to false formula.
3. Using the fact that falsehood implies everything, use 2. to derive the desired conclusion (preferably not going through too many obviously false statements).

This method is especially effective late at night or after a few drinks (or, even better, late at night and after a few drinks). The reason why I have not yet published solutions of any of the big open problems in mathematics is that next morning I would look at my notes and check for errors with fresh eyes and using some common-sense heuristics I've picked up over the years. If the solution still looks hopeful I would show the argument to a colleague or two over coffee or send them a quick email, thus limiting my embarrassment when the error is inevitably found to just a handful of people. In the unlikely case where these filters fail, I would rigorously write up the argument and send it to a journal (or - more likely - try and fail to write it up, and stop there). Once the paper is rejected, I would take the feedback seriously, and most likely realise why my approach fails, and switch to thinking about something else.

These filters are often not going to be available to a non-academic. Many of them result from making errors and getting them shot down by your supervisor or teacher at some relatively early point in your career. Like Feynman said, "The first principle is that you must not fool yourself, and you are the easiest person to fool."

Answer 11

To complement what the others said here is one more issue. Let's say they work hard and in their random movements they stumble on something interesting. Will it be new? The answer is probably no. Unless you know the current state of the art you are most likely going to reinvent the wheel (if you are going to invent something useful at all). The "independent researcher" has almost never put in the work to understand what the cutting edge of research in the area is and what questions they could investigate that give new interesting results. This requires a formal education they almost always lack.

Answer 12

The core answer to your question is simple: cutting-edge research in physics (or any other field) is very difficult. It is sooooo easy to make a simpler error and there is nothing like an undetected error to make a computation look like a discovery.

It is almost a self-evident truth to professional researchers that research is largely about failure management. Almost everything I try ends up in a dead-end, but on occasions something sticks and is worth investigating in greater depth. The advantage I have over wannabe physicists is the network of colleagues and collaborators to help me detect errors - simple, hard, not obvious, obvious. Sometimes it’s just a sign error. Sometimes it’s just a typo in a line of code. I dunno of any successful researcher working in isolation: you need the possibility of discussing with others to quickly eliminate the 10 most obvious errors and restrict the possible path to solution.

Most students and other non-professionals are not smarter than their supervisors yet they do not perform at the same level precisely because they haven’t mastered the art of detecting and recovering from errors in their own work. They have an overly narrow understanding of the problem they are working on, and maybe the pet theory solves one specific problem but it is easily disproved by data or doesn’t explain another effect.

Answer 13

You have to learn to crawl before you learn to walk, and you have to learn to walk before you learn to run.

The people you speak of don't know how to crawl but try to be Usain Bolt. Their failure is a foregone conclusion.

Answer 14

To summarise in two words all of the other answers in the shortest answer here ...

Dunning, Kruger

Answer 15

As one who has both wasted time publishing poor research on the shoulders of giants and also wasted time getting nowhere with what I know in my mind and heart should stand on its merits and quality, I have some insight to offer.

First, those formal academic qualifications mean something. What goes into research (asking good questions, finding a strategy to answer them, finding and using qualified sources, overall good methodology) is not intuitive. Anyone who went through the process of earning those credentials has a good understanding of what research means and how to execute it. Becoming a good researcher is not just about assembling information, that's easy to do in an information world. It's about what to do with it.

Second, the process of becoming a professional and professional puts individuals in contact with others who inform and support them in their work. Collective bodies of knowledge and best practice evolve and shift. Just think about how much citations have changed in just a few years. When your work gets to an editor and bounces off three expert peer reviewers who speak the same language, know how to advise, and might even recognize the voice (in what should be a blind process), it needs substance to push through and be heard.

Third, the culture of academia and human nature make it difficult to succeed in a venue where others have credentials and find it threatening for someone to come along and present good work. You can see this over and over again. You could write the greatest novel every penned, but even in this information world with a possibly more level playing ground, you probably won't get picked up by a major publishing house.

That last point is well illustrated within these pages. If you could somehow see all the thoughtful, important questions--and valid answers--that have been deleted before their time, you would understand get a good lesson in the psyche and politics of institutions of higher education. But read fast, you might not see this in 12 hours...

Answer 16

Suppose that someone is in a course, say for mathematics, then the only way they can pass is if they show performance to the expectations of pre existing mathematicians, that is, present the answers in a way that others also accept it.

This means, if one is to succeed in such a course, then it shows an ability to conform.

Conforming is usually used in a negative sense, but here, in my opinion, it is a positive thing to conform.

Nonetheless, a person who hasn't gone through such a course would never face criticism virtue of non conforming unless they had a community of people to help them out.... which... If you think about it, is simply a simulation of a university esque environment.

Of course, if someone grew up in a different environment then that in itself is simply no reason to stereotype them. Such type of situations were also the ones conducive to phenomena such as development of dialects of a language.

I personally like to believe, that there is a standard of truth in science relative to which, we can judge any given statement for it's truth. In principle, one should be able to distinguish trueness or a lack of by this standard.

The role of the university would then be to make sure that those who obtain the degree have also acquired the conscience to judge statements by this standard as well.

Then the problem of a non academic researcher would be that they simply don't keep the ideas they propagate to this standard.

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Note: the answer is based on a highly idealistic views of university and education. Considering real life experiences this turns from a strong to a very weak arguement.

Answer 17

Einstein managed to publish his doctoral thesis (which almost nobody cares about today) the same year as those other four little papers. He was not able to do this because of his towering intellect (though it was) or his academic advisors (who were helping him on his thesis). He did it for the same reason that Newton and Gauss could discover so many things on their own: theirs were fundamentally human sized problems. Humans have been picking over challenging problems in a somewhat systematic way for at least five hundred years, and if a big problem could be solved with a single intellect, it's a safe bet that it has.

We live in an era where the two options for solving big problems are to find a new or obscure field with few competing scholars or to work in large teams. Having advisors point out your flaws (of which, there will be many), direct your efforts and provide feedback all helps, but even the "small" problems of doctoral theses are at the outer limit of what a single human can do these days. We all stand on the shoulders of giants today, but that means our achievements look like the buttons on those giants coats... small. Unfortunately, the narrative about what's possible with research hasn't changed since the time of Einstein, so people without a formal connection to academia have both the wrong idea about what's possible and the burden of striving alone.