My field is theoretical physics, so this is where my views come from. (Disclaimer: I have not had a research position since finishing my PhD in General Relativity some 10 years ago.) Assuming you want to do original research, and you are not a genius like Feynman (in which case you would not be interesting in my views, anyway, what do you care what other people think?):
Map the landscape first. What is known, which areas of research are active, which are inactive. No need to go super deep, just get the feel for what is where.
Gain the basic understanding of why the landscape is the way it is. Why are certain areas being worked on? Is it fashion, ease of progress, tradition, something else? Why are certain areas being ignored or stagnate? Are they too hard, too boring, unlikely to get you a research position, just overlooked, or something else?
Find a promising area which is not well researched, does not appear super hard, yet you find interesting. Interdisciplinary outlook could be useful.
Figure out what you are missing to do a meaningful original contribution there. Evaluate what it would take to learn the prerequisites. Alternate between learning and trying to push the original research.
Most likely you will gain unexpected insights, not into the problem you are trying to solve, but into the reason why it’s not being actively worked on. Go back and reevaluate whether the area is still promising and interesting. Odds are, your new perspective will lead you to get excited about something related but different.
Repeat until you are sure that you have learned something no one else has. Whether a question no one asked, or a model no one constructed or applied in this case, or maybe a map from a completely unrelated area.
Do a thorough literature search on the topic. Odds are, you will find that someone else tried it already. Reevaluate. Iterate.
Eventually you might find something where you can make a useful original contribution, no matter how small. Or you might not. Still, you will likely end up knowing more and having a valuable perspective and a skill set.
Physics examples: don’t go into QFT, String theory or Loop quantum gravity. No way you can do better than, say, Witten and Maldacena and thousands of theorists with IQ 150+ and the energy and determination of a raging rhino. Quantum foundations might still have some low-hanging fruit, but the odds are against it. No idea about the condensed matter research. A positive example: Numerical relativity hit a sweet spot about 15 years ago, because the compute and the algorithms converged, and there were only a few groups doing it. Odds are something similar is possible again, just need to find where.
Also, Kaj, your research into multi-agent models of the mind, for example, might yield something really exciting and new, if looked at in a right way, whatever it is.
My field is theoretical physics, so this is where my views come from. (Disclaimer: I have not had a research position since finishing my PhD in General Relativity some 10 years ago.) Assuming you want to do original research, and you are not a genius like Feynman (in which case you would not be interesting in my views, anyway, what do you care what other people think?):
Map the landscape first. What is known, which areas of research are active, which are inactive. No need to go super deep, just get the feel for what is where.
Gain the basic understanding of why the landscape is the way it is. Why are certain areas being worked on? Is it fashion, ease of progress, tradition, something else? Why are certain areas being ignored or stagnate? Are they too hard, too boring, unlikely to get you a research position, just overlooked, or something else?
Find a promising area which is not well researched, does not appear super hard, yet you find interesting. Interdisciplinary outlook could be useful.
Figure out what you are missing to do a meaningful original contribution there. Evaluate what it would take to learn the prerequisites. Alternate between learning and trying to push the original research.
Most likely you will gain unexpected insights, not into the problem you are trying to solve, but into the reason why it’s not being actively worked on. Go back and reevaluate whether the area is still promising and interesting. Odds are, your new perspective will lead you to get excited about something related but different.
Repeat until you are sure that you have learned something no one else has. Whether a question no one asked, or a model no one constructed or applied in this case, or maybe a map from a completely unrelated area.
Do a thorough literature search on the topic. Odds are, you will find that someone else tried it already. Reevaluate. Iterate.
Eventually you might find something where you can make a useful original contribution, no matter how small. Or you might not. Still, you will likely end up knowing more and having a valuable perspective and a skill set.
Physics examples: don’t go into QFT, String theory or Loop quantum gravity. No way you can do better than, say, Witten and Maldacena and thousands of theorists with IQ 150+ and the energy and determination of a raging rhino. Quantum foundations might still have some low-hanging fruit, but the odds are against it. No idea about the condensed matter research. A positive example: Numerical relativity hit a sweet spot about 15 years ago, because the compute and the algorithms converged, and there were only a few groups doing it. Odds are something similar is possible again, just need to find where.
Also, Kaj, your research into multi-agent models of the mind, for example, might yield something really exciting and new, if looked at in a right way, whatever it is.