Big Questions

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.

Imagine how strange, then, the real world seems to me.  For example, Caltech prof and top science blogger Sean Carroll publishes a well-written book, From Eternity to Here, arguing for his explanation for the arrow of time, clearly one of our deepest questions.  Yet not only are such attempts rare, they get surprising little engagement.  Of the fourteen other blurbs, reviews, and articles (besides mine) listed at the book website, none express an opinion on whether Carroll’s answer is right, much less offer reasons for such an opinion.  Of the six Amazon reviews, two do express an opinion, one by complete-crank Ranger McCoy, and one by Lubos Motl, who says there is no arrow of time problem.  I also found a review by Peter Woit, who rejects the whole idea of a multiverse.  Geez, what does it take to get serious engagement of a proposed answer to a deep question?

If you search for “arrow of time” or “origin time asymmetry” at you’ll find a smattering of papers, but almost no one makes the subject their main focus.  In our real intellectual world, smart ambitious folks find it far easier to signal their ability by working on more mundane ground work or practical questions.  So only a crank focuses their effort on a deep question, inducing people afraid of being confused with cranks to be careful to avoid such questions.  Super bigshots sometimes counter-signal, rambling on about such topics without having given them much thought, just to show that they can.

Kudos to Sean for bucking the trend, and I hope he gets more serious engagement sometime soon.  As I said, his story is consistent, if speculative:

Many of these are far-from-proven conjectures, but still it does all hold together. … Even so, it is very hard to over-emphasize just how far one must project current physics beyond the accuracy with which we have verified it to talk about tiny new universes popping out of quantum fluctuations in empty space at 10-29K.

In the social sciences books that propose answers to deep questions do at least get reviews that engage those proposed answers.  Is that because we actually care more about social science questions?

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  • Millian

    Do giants live in the Amazon?

  • david

    Philosophers don’t seem disinclined to engage directly with the hard stuff.

    Could it be a problem limited to physics? It has the twin blows of

    1) being convincingly “mostly right”, making leaving the beaten track unattractive and unnecessary for most work, and
    2) a (cultural?) focus on ‘making the math work’ rather than affixing an interpretation

    There’s that Feynman quote – “Do not keep saying to yourself, if you can possibly avoid it, ‘But how can it be like that?’ because you will get ‘down the drain’, into a blind alley from which nobody has yet escaped. Nobody knows how it can be like that”.

  • Tyrrell McAllister

    I’m having trouble grasping what you consider to be the “deepest most important questions”.

    But I think that you answer your own question when you write, after summarizing his view, that “It will be truly incredible if we get that right.”. That amounts to saying that he constructed a theory that is almost certain to be wrong. Why would someone want to do that?

  • Richard Hamming, in his great lecture “You and Your Research“, gives an example of how uncomfortable the idea of “big questions” makes some researchers:

    Over on the other side of the dining hall was a chemistry table. … I went over and said, “Do you mind if I join you?” They can’t say no, so I started eating with them for a while. And I started asking, “What are the important problems of your field?” And after a week or so, “What important problems are you working on?” And after some more time I came in one day and said, “If what you are doing is not important, and if you don’t think it is going to lead to something important, why are you at Bell Labs working on it?” I wasn’t welcomed after that; I had to find somebody else to eat with!

    • “If what you are doing is not important, and if you don’t think it is going to lead to something important, why are you at Bell Labs working on it?”

      A good response would be that it would be useful or at least I can make some progress on this question. Attacking questions that you can’t actually make progress on is a mark of immaturity, persisting at it is either the mark of, or turns one into, a crank.

  • mjgeddes

    Well, we are motivated by feelings, and some feelings have greater salience for the human mind than others.

    Economics is going to provoke the social emotions:

    Confidence, Fear, Benevolence, Anger, Respect, Contempt, Pride, Shame, Delight, Sadness, Connectedness, Angst

    Physics is going to trigger a more abstract set of feelings, what I call the ‘intellectual emotions’:

    Recognition, Puzzlement, Curiosity, Boredom, Understanding, Confusion, Discernment, Frustration, Clarity, Doubt, Wonder, Disenchantment

    But this latter set of feelings is much more weakly hard-wired into the human brain. Everyone the feels the social emotions strongly, but the latter set of intellectual emotions only seems to appeal to a small percentage of people, who I hypothesize, are cognitively abnormal (by a quirk of the genes they are among the few feeling these emotions strongly). These are the sci-fi writers, transhumanists etc. 😉

  • Robert Koslover

    You said: “Aspiring to high status, I also tried to identify and chip away at deep questions.” I hear you, dude. Been there, done that, and… gave it up. Why? Because I eventually, and somewhat painfully, concluded that such problems were better left for people with more powerful brains than my own. It seems to me that one top-notch (and I mean top-notch!) theoretical physicist can generally accomplish as much as perhaps fifty (or even more) rather-ordinary theoreticians. So, why be a part of the mostly-unknown (and minimally-contributing!) theorist herd? Don’t get me wrong – I really do admire that theoretical herd, especially for their being willing to work so very hard to understand and contribute to a subject that is, quite frankly, often beyond their mental abilities. But the deepest questions in physics are probably best left to those at the highest tier. Again, not because those of us at one, two, or even three levels below that can’t understand those questions and/or appreciate the beautiful theoretical answers to them, but rather that committing our careers to attacking those kinds of questions is simply a waste of resources. As an applied electromagnetics physicist, I am confident that I now contribute far more to the world of science & engineering than I would have as a (likely quite ordinary) theoretical particle physicist. To quote the popular philosopher Clint Eastwood (Magnum Force, 1973), “a man’s got to know his limitations.”

    • michael vassar

      How large are the levels you are discussing?

      IMHO, it seems to me that almost everyone in our society, in science or out, works on subject matter a little out of their depth. Maybe everyone should downshift by one subject.

  • I’m not sure this is a mundane vs. big split. Most of the physics books in B&N aren’t on mundane topics at all. Most are big-theory books, not a book like The Economic Naturalist that explains how we calculate the speed limit for rounding a turn, etc., like on Mr. Wizard’s World or Bill Nye the Science Guy or Beakman’s World.

    Same is true for the philosophy section, or literary theory, and so on. The social sciences are the only section I can think of where there’s a decidedly mundane and practical focus.

    It’s just that the abstract topics that the physics, philosophy, etc., sections look at aren’t those that interest the crowd, like the arrow of time might interest them. Literary theory could be abstract, like is the list of narratives open-ended or mostly variations on a small set of themes? And if the latter, why those themes instead of others? Instead, it’s abstract stuff about how some poet subverted the imperialist meta-narrative by transgressing the ethno-poetics of binariality.

    Philosophy and physics used to have a healthy emphasis on the mundane too — how to live a good life, how to make eyeglasses, etc.

    Now they’ve junked the practical and favor Big Pointless Questions over Big Interesting Questions. Now that the public has access to responses on the interesting big questions, the status-seeking academics have to focus on the pointless big questions to distinguish themselves.

  • david, yes philosophers seem the main exception.

    Tyrrell, even if that specific story is wrong, a similar story may be right.

    Mark, yes, Hamming puzzled over the same thing.

    Robert, sure top folks are more productive, but it is not clear they have a stronger advantage on these questions than any others. Few top folks tackle those questions, so if we leave it to them, it won’t get done.

    agnostic, there’s a big difference between books that review big questions, and books that propose original answers.

  • Robert Ayers

    I agree with the interesting premise of Robin’s article, but the example is not compelling.
    I decided that time-asymmetry and the second law of thermodynamics were no longer a “deep important question” after I read “The Physics of Time Asymmetry” by P C W Davies — because Davies explained it to me.
    (Davies did not have to appeal to cosmology, so maybe the Carroll book is addressing a different problem.)

    • Bo

      Gary Drescher’s “Good and Real” does a good job of demystifying the problem as well.

  • Michael Turner

    Theoretically, science deals in theoretically falsifiable propositions. Practically, it deals in practically falsifiable ones. Sean Carroll seems to admit frankly that his theory is not practically falsifiable.

    A question often remains big and important because it’s very hard — so much so that it appears to be impractical (in professional terms) to spend much of one’s career attempting to decide the issue, especially those make-or-break tenure-track years. Hence, in computer science, back in 1977, we saw a paper titled “The graph isomorphism disease”, a statement of exhaustion, and a warning beacon to fresh minds in the field of graph theory.

    To the extent that academia is darwinian (significantly, I think), and to the extent that any darwinian scheme relies on reproductive fitness (again, I think significantly in the case of academia), a reasonable citation index is more likely to be earned by encouraging one’s graduate students to focus on the more obviously workable veins of the salt mines.

    Remember, there’s real life to be considered here, including *real* reproductive fitness, not just how prolific one is in terms of Minimum Publishable Units and citations thereof. A friend of mine once promised his wife that she could have a second child with him IF he got tenure. (Yes, he got tenure, and Yes, they had the kid, but No, he didn’t do it by proving anything about the tractability of testing for graph isomorphism.)

  • Robin, you suggest that this book tackles an important question, and provides an original answer. And you wonder why you don’t see more serious responses.

    But don’t you find it odd that the form of the work was as a popular science book for lay audiences? Non-physicists, even non-scientists are picking up this book and “learning” something.

    Surely the most qualified responses would be from other physicists who have also worked in this area. But Carroll didn’t write a document addressed to them. Why not?

    It reminds me instead of cold fusion: if the idea isn’t solid enough to confront knowledgeable critics, then just skip over them and address your remarks to ignorant readers instead. Surely you’ll get a more sympathetic reaction.

    I’m saying this without having read the book or addressing the content at all. But don’t you find the form of a popular book, for presenting a new idea on a deep question in physics, to be at all suspicious?

  • improbable

    I think you’re underestimating how much work is motivated by the desire to answer such questions. The paper might make no mention of (say) the arrow of time, but nonetheless the reason the author has chosen to devote years to some topic which may be relevant to “answering” this question may well be that he/she finds the big question interesting.

    Very few big questions are open to direct attack. Or rather, the fact that they are still unsolved big questions means that all the direct lines have been tried (written about) and found wanting.

    So if you want to help our understanding of consciousness, you shouldn’t write philosophy papers about consciousness, but rather dive into some area of cognitive/neuroscience, and try to push that forwards. Likewise if you want to understand what spacetime really is, you should dive into some corner of string theory, and do the same. With luck you’ll be around to see progress in these more technical fields lead to a better understanding of the big question.

    This has happened with both of these examples, but slowly, incrementally, and without there being some paper about the big question itself which you could point to as the source. The papers (or books) about the big question tend to be written after the fact, summaries for non-experts of what shift in understanding has already occurred for those who were following the technical details.

  • Tim Tyler

    I’m with Lubos Motl’s Amazon review.

  • Robert, I think you misunderstood Davies.

    Don, he does also have papers on this.

    Improbable, yeah people say they are working indirectly on the big questions, but if so you’d think they’d pay lots of attention to proposals to build an answer from their ground work.

    Tim, yes, we could tell.

    • improbable

      “if so you’d think they’d pay lots of attention to proposals to build an answer from their ground work”

      I wonder about this too. You seem to conclude that they are being dishonest about their motivations, and are really in the game for status. I agree that some are, but not all. I think that those who are serious tend to be writing off such attempts, generally with good reason.

      If you’re inside a technical field which touches on a “big question” like this, and you care, you do hold up new technical progress to see what it tells you about the big question. You tend to know which technical questions would, if answered, lead to how much progress on the big question. And when it emerges that we have in fact solved the big question, it’s not that someone from outside comes in and builds on your technical work to write a solution. It’s more like that everyone just gradually agrees that this is done, there is no longer anything deep left there.

      For instance this happened with the interpretation of quantum mechanics. This used to be a “big question” but then gradually we got better at understanding how decoherence worked, and did cleaner and cleaner experiments, until more and more people who cared about the question simply agreed that there wasn’t anything else left to know. I guess this is a bit anticlimactic but that’s how it is.

      • Interpretation of quantum mechanics definitely counts as an open big question – if you think it is resolved you don’t understand it.

      • improbable

        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.)

  • Grant

    Why would we want to fund research into these questions? We don’t have any practice use for answers to them. Most philosophical questions (and probably most physics questions?) can be pondered and solved with no funding whatsoever, so I can’t see why we’d want to fund academics to do so.

    Besides, what makes these questions “deep”? If our intuition is to value “deep” answers over practical ones, might there be something irrational about this intuition?

    I am not trying to say thinking about big questions is wasteful, but it seems rational that we devote little resources to them. Like ‘big ideas’, they seem to be cheap to develop and of little practical use at the time.

    • Jayson Virissimo

      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).

  • Haven’t read the book I’m afraid, so I don’t know if it relates to Zeno’s paradoxes. Could one answer to Achilles and the tortoise be that space-time is granular rather than a smooth continuum?

  • Hal Finney

    Seems to me there are two kinds of hard problems. One is cases where there are many possible solutions and it is hard to come up with ways to test and distinguish them. The other is cases where there seem to be no solutions that work well. Consciousness would be an example of the second (IMO). Gravitational theory would be an example of the first. Which category (if either) would the arrow of time fall into?

    • improbable

      Hal Finney:

      I think the arrow of time (in Carrol’s sense, of why the universe started so simple) is probably a hard question with no good answers yet. Although I haven’t yet thought hard about his proposals.

      But Gravity (meaning quantum gravity plus dark energy I suppose) I would certainly put in your second category, there are very few proposals without glaringly huge problems.

      Consciousness is more slippery, my reading of what we’re learning is that it’s more like the once-big question of Life — we’ve learned a lot about how life works, to the point where the big question of 100 years ago seems a little silly now.

    • mjgeddes

      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.

  • aram

    Science is incremental. Working on small problems can be the best way to solve big problems. In fact, often we care about big problems _because_ they yield progress on many small problems; e.g. proving Fermat’s last theorem was exciting to mathematicians not because we really needed to know whether x^r + y^r = z^r had any solutions, but because lots of other math got invented along the way.

    Terry Tao–who is smarter than any of us–explains more at this link.

  • Matt

    A few years back when there was all the debate about whether we should teach evolution or creationism, there was a side debate about how fundamental Christians believed the world began 3,000 years and how scientists believe it’s billions of years old. I never heard anyone even entertain the idea that they might both be right, and that was extremely dissapointing for me.

  • Abhinav


    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.”

    • 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.

      • Abhinav

        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?

      • Jayson Virissimo

        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)?

  • Doug S.

    What Abhinav said.

    What are the engineering applications of knowing the answer to the arrow of time problem?

    • Hal Finney

      You can make sure that your machines don’t accidentally cause the arrow of time to run backwards… 🙂

  • Jason

    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”.)

  • Jess Riedel

    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?

  • 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.

    • 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?

  • 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.

  • John

    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.