When young, I imagined that the giants of the intellectual world would be found chipping away at our deepest most important questions. Sure perhaps most intellectuals would work on practical problems with paying customers, or do less glorious but needed ground work, but the best and the brightest would focus on combining that ground work into deep answers. Aspiring to high status, I also tried to identify and chip away at deep questions.
Congratulations! You have arrived. Only someone who has truly overcome all human bias could be blind to—and even a bit exasperated by—why we care more about social science.
Hint: It’s common sense, but scientists can explain it too.
Or are you feigning dismay for rhetorical purposes and maybe a tad of status signaling? Same as if I were to express dismay at how little people care about “important,” “deep” contemporary art.
We don't know know how to experimentally test ANY elements of it. I read Carroll's book, looking carefully for any sort of way of testing, even in principle, his multiverse explanation of the arrow of time, and found nothing. This is the same problem shared by most multiverse explanations of "deep questions" in physics. There are some multiverse models that, at least in principle make some sort of prediction, perhaps of a statistical nature. In those cases you need to look more deeply at whether the model can really predict anything.
Actually I don't reject the possibility of a multiverse, just point out that if you want to invoke this as a scientific explanation, you need some sort of conventional scientific evidence, or at least a plausible way to get some in principle. Absent this, you just have an empty, untestable "explanation" which may make you happy, and may sell books, but is not something that most scientists will take seriously. This point of view on the multiverse matter I suspect is shared by the great majority of physicists.
I see no shortage at all of people working on and writing about "deep questions" in physics. I hear from a couple of them a day. The problem is that they're almost all cranks. There are plenty of physicists and other scientists who put a lot of their time and energy into thinking about the deep questions of their subject. The really good ones though are intensely aware of how difficult it is to make real progress on these questions (if you don't invoke the multiverse...) and see no point to either publishing their ideas that have led nowhere, or writing critiques of other people's such ventures.
But more on topic, I would be interested to hear your examples of Big Questions which has been solved in the manner you suggest: where a person (or a paper) takes all the technical progress and uses it to answer the big question, in a way that the technical people had missed.
I think that consciousness, and nurture-nature, and the nature of spacetime, are examples of big questions in which we're making the kind of progress I'm describing. (Sadly I don't know economics well enough to know examples there.)
The arrow of time is a deep problem which almost certainly requires a good knowledge of modern physics to answer. Why, then, is Carroll writing about his proposed speculative solution in a book aimed at the laymen? Even if his peers refuse to engage his reasoning (have they? has this stuff been published anywhere else besides the ArXiv?), why should he write for the general public, who aren't educated enough to judge the merits of his work?
It seems likely here that Carroll has proposed a solution which could be correct but is *not* obviously so and resists any experimental testing. What do you expect physicists to do?
One possible explanation is that the literature retains a bias towards answering small questions precisely becase they are small. You can answer them and write a paper. Big questions are in a sense big because they haven't been solved.
Take one: Why is the Earth here? That would have been a big question at one time. Well, once you have the big bang nucleosynthesis, elements and such, it really turns out to be a practical question of solar system formation.
In my own personal journey through physics, my original papers started somewhat small -- beginning with nuclear dynamics -- but I did have an overarching "big question" in my head the entire time I was in grad school: "Solving" non-perturbative QCD. Of course I didn't solve that one (yet), and I still have some ideas about intermediate "interpolating" field theories between the asymptotically free high energy QCD and low energy chiral perturbation theory. The light of the "big problem" at the end of the tunnel lead me to a pretty interesting model of the quark struture of nuclei that shed some light on a long standing problem in the field. I was able to make some progress and write some papers.
This is probably similar to the others who described the big problems as too hard and too daunting to just directly tackle. But I think more people are thinking about these big problems while making steps, but just leave their speculations out of their papers. I know I did for the most part -- partially out of fear of looking foolish, partially out of fear of having my ideas co-opted by another, and partially out of what's necessary to publish a paper in a journal.
As an aside, I think Raphael Bousso, Leonard Susskind, Ben Frievogel, et al are doing work that encompasses some of Sean Carroll's ideas. Entropy, causality, Boltzmann brains and the like are all relevant. (Susskind et al have a particularly interesting 2D holographic theory that has an emergent time and one emergent space dimension. Search the arXiv for the "Census Taker".)
I think it should be stated what the big problems actually are. So here are 10 ‘Big Problems’ for the new decade. There is plenty of glory for the ‘big shots’ here.
Consciousness (cognitive science)
Resolving the most personal of mysteries, we would have a map of our own minds, in the form of either a fundamentally new metaphysics and/or a new way to understand information and communication.
Values (cognitive science)
Understanding the existence (or non-existence) of social and/or human and/or platonic values and their characteristics would either provide a firm secular foundation for our belief systems or a rational basis for new theologies.
Intelligence (cognitive science)
The key to rationally achieving goals would provide ultimate power, illuminating the foundations of science itself. Understanding self-improving intelligence would assist a possible ‘intelligence explosion’ and the creation of artificial intelligences exceeding human abilities.
Interpretation of QM (physics)
Understanding the connection between pure theory and empirical observables would resolve the nature of abstract entities and ‘possible’ worlds, providing a deep metaphysics for existence itself and possibly new anthropic principles to help explain our place within it.
Unified Field theory (physics)
Integrating all the forces of nature into a single framework would end fundamental physics in a triumph of reductionism, finding the equations and basic building blocks for the base level of reality. Or, showing this was not possible would usher in a new type of non-reductionist metaphysics.
The arrow of time (cosmology)
Understanding the apparent flow of time would illuminate the most basic principles of applied physics (thermodynamics) and provide deep insights into the very origin of the universe itself, its evolution and possibly even its purpose (if any).
Dark matter and dark energy (cosmology)
Understanding the nature of dark energy would reveal the ultimate fate of universe and possibly usher in new physics that could be harnessed for space travel and further understanding of astrological phenomena.
Origin of life (biology)
Grasping our origins would expose the deep principles behind life itself, providing deep insights into our own natures and the natures of other living things.
Extra-terrestrial life (biology)
Finding extra-terrestrial would provide deep new insights into biology as well as revising our understanding of our own place in the cosmos and reinvigorating interest in science and exploration.
Riemann Hypothesis (mathematics)
Understanding prime numbers would rock the foundations of mathematics itself, revising our understanding of mathematics across the board, even of the most basic operations such the relation between multiplication and addition.
In medieval Europe, one of the key questions was to determine the number of angels which could dance on a pinhead.
Do you have any decent evidence for this claim, or are you just one of those people that believes everything in their university science textbook (like that people in the Middle Ages thought the world was flat)?
Why would we want to fund research into these questions? We don’t have any practice use for answers to them.
Perhaps you are familiar with different disciplines than I am, but in economics, political science, and sociology, many of the problems that researchers are trying to solve aren't even worth the effort (and especially not the financial resources that go into them).
In medieval Europe, one of the key questions was to determine the number of angels which could dance on a pinhead. How much should I be interested in a claimed answer to that question? Is Sean just another monk with an answer where nobody can make any experimental observations about the angels or is he a Boltzmann? How do we tell the difference before somebody makes the right connections with experiments?
Not being able to think of how to attack a big question might well make you not want to attack it, but that doesn't explain your disinterest in someone else's claimed answer.
Someone in the thread mentioned Hamming and his famous speech. I'll quote a different section which talks about important problems.
"Let me warn you, `important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important."
Peter Medawar also talked about this."Good scientists study the most important problems that they think they can solve. It is, after all, their professional business to solve problems, not merely to grapple with them."
Congratulations! You have arrived. Only someone who has truly overcome all human bias could be blind to—and even a bit exasperated by—why we care more about social science.
Hint: It’s common sense, but scientists can explain it too.
Or are you feigning dismay for rhetorical purposes and maybe a tad of status signaling? Same as if I were to express dismay at how little people care about “important,” “deep” contemporary art.
We don't know know how to experimentally test ANY elements of it. I read Carroll's book, looking carefully for any sort of way of testing, even in principle, his multiverse explanation of the arrow of time, and found nothing. This is the same problem shared by most multiverse explanations of "deep questions" in physics. There are some multiverse models that, at least in principle make some sort of prediction, perhaps of a statistical nature. In those cases you need to look more deeply at whether the model can really predict anything.
To be clear, you don't think Carroll's proposal worth critiquing more because we do not yet know how to experimentally test all elements of it?
Actually I don't reject the possibility of a multiverse, just point out that if you want to invoke this as a scientific explanation, you need some sort of conventional scientific evidence, or at least a plausible way to get some in principle. Absent this, you just have an empty, untestable "explanation" which may make you happy, and may sell books, but is not something that most scientists will take seriously. This point of view on the multiverse matter I suspect is shared by the great majority of physicists.
I see no shortage at all of people working on and writing about "deep questions" in physics. I hear from a couple of them a day. The problem is that they're almost all cranks. There are plenty of physicists and other scientists who put a lot of their time and energy into thinking about the deep questions of their subject. The really good ones though are intensely aware of how difficult it is to make real progress on these questions (if you don't invoke the multiverse...) and see no point to either publishing their ideas that have led nowhere, or writing critiques of other people's such ventures.
Well then we disagree about QM.
But more on topic, I would be interested to hear your examples of Big Questions which has been solved in the manner you suggest: where a person (or a paper) takes all the technical progress and uses it to answer the big question, in a way that the technical people had missed.
I think that consciousness, and nurture-nature, and the nature of spacetime, are examples of big questions in which we're making the kind of progress I'm describing. (Sadly I don't know economics well enough to know examples there.)
Gary Drescher's "Good and Real" does a good job of demystifying the problem as well.
The arrow of time is a deep problem which almost certainly requires a good knowledge of modern physics to answer. Why, then, is Carroll writing about his proposed speculative solution in a book aimed at the laymen? Even if his peers refuse to engage his reasoning (have they? has this stuff been published anywhere else besides the ArXiv?), why should he write for the general public, who aren't educated enough to judge the merits of his work?
It seems likely here that Carroll has proposed a solution which could be correct but is *not* obviously so and resists any experimental testing. What do you expect physicists to do?
One possible explanation is that the literature retains a bias towards answering small questions precisely becase they are small. You can answer them and write a paper. Big questions are in a sense big because they haven't been solved.
Take one: Why is the Earth here? That would have been a big question at one time. Well, once you have the big bang nucleosynthesis, elements and such, it really turns out to be a practical question of solar system formation.
In my own personal journey through physics, my original papers started somewhat small -- beginning with nuclear dynamics -- but I did have an overarching "big question" in my head the entire time I was in grad school: "Solving" non-perturbative QCD. Of course I didn't solve that one (yet), and I still have some ideas about intermediate "interpolating" field theories between the asymptotically free high energy QCD and low energy chiral perturbation theory. The light of the "big problem" at the end of the tunnel lead me to a pretty interesting model of the quark struture of nuclei that shed some light on a long standing problem in the field. I was able to make some progress and write some papers.
This is probably similar to the others who described the big problems as too hard and too daunting to just directly tackle. But I think more people are thinking about these big problems while making steps, but just leave their speculations out of their papers. I know I did for the most part -- partially out of fear of looking foolish, partially out of fear of having my ideas co-opted by another, and partially out of what's necessary to publish a paper in a journal.
As an aside, I think Raphael Bousso, Leonard Susskind, Ben Frievogel, et al are doing work that encompasses some of Sean Carroll's ideas. Entropy, causality, Boltzmann brains and the like are all relevant. (Susskind et al have a particularly interesting 2D holographic theory that has an emergent time and one emergent space dimension. Search the arXiv for the "Census Taker".)
I think it should be stated what the big problems actually are. So here are 10 ‘Big Problems’ for the new decade. There is plenty of glory for the ‘big shots’ here.
Consciousness (cognitive science)
Resolving the most personal of mysteries, we would have a map of our own minds, in the form of either a fundamentally new metaphysics and/or a new way to understand information and communication.
Values (cognitive science)
Understanding the existence (or non-existence) of social and/or human and/or platonic values and their characteristics would either provide a firm secular foundation for our belief systems or a rational basis for new theologies.
Intelligence (cognitive science)
The key to rationally achieving goals would provide ultimate power, illuminating the foundations of science itself. Understanding self-improving intelligence would assist a possible ‘intelligence explosion’ and the creation of artificial intelligences exceeding human abilities.
Interpretation of QM (physics)
Understanding the connection between pure theory and empirical observables would resolve the nature of abstract entities and ‘possible’ worlds, providing a deep metaphysics for existence itself and possibly new anthropic principles to help explain our place within it.
Unified Field theory (physics)
Integrating all the forces of nature into a single framework would end fundamental physics in a triumph of reductionism, finding the equations and basic building blocks for the base level of reality. Or, showing this was not possible would usher in a new type of non-reductionist metaphysics.
The arrow of time (cosmology)
Understanding the apparent flow of time would illuminate the most basic principles of applied physics (thermodynamics) and provide deep insights into the very origin of the universe itself, its evolution and possibly even its purpose (if any).
Dark matter and dark energy (cosmology)
Understanding the nature of dark energy would reveal the ultimate fate of universe and possibly usher in new physics that could be harnessed for space travel and further understanding of astrological phenomena.
Origin of life (biology)
Grasping our origins would expose the deep principles behind life itself, providing deep insights into our own natures and the natures of other living things.
Extra-terrestrial life (biology)
Finding extra-terrestrial would provide deep new insights into biology as well as revising our understanding of our own place in the cosmos and reinvigorating interest in science and exploration.
Riemann Hypothesis (mathematics)
Understanding prime numbers would rock the foundations of mathematics itself, revising our understanding of mathematics across the board, even of the most basic operations such the relation between multiplication and addition.
In medieval Europe, one of the key questions was to determine the number of angels which could dance on a pinhead.
Do you have any decent evidence for this claim, or are you just one of those people that believes everything in their university science textbook (like that people in the Middle Ages thought the world was flat)?
Why would we want to fund research into these questions? We don’t have any practice use for answers to them.
Perhaps you are familiar with different disciplines than I am, but in economics, political science, and sociology, many of the problems that researchers are trying to solve aren't even worth the effort (and especially not the financial resources that go into them).
You can make sure that your machines don't accidentally cause the arrow of time to run backwards... :)
What Abhinav said.
What are the engineering applications of knowing the answer to the arrow of time problem?
In medieval Europe, one of the key questions was to determine the number of angels which could dance on a pinhead. How much should I be interested in a claimed answer to that question? Is Sean just another monk with an answer where nobody can make any experimental observations about the angels or is he a Boltzmann? How do we tell the difference before somebody makes the right connections with experiments?
Not being able to think of how to attack a big question might well make you not want to attack it, but that doesn't explain your disinterest in someone else's claimed answer.
Robin
Someone in the thread mentioned Hamming and his famous speech. I'll quote a different section which talks about important problems.
"Let me warn you, `important problem' must be phrased carefully. The three outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn't work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It's not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important."
Peter Medawar also talked about this."Good scientists study the most important problems that they think they can solve. It is, after all, their professional business to solve problems, not merely to grapple with them."