Thursday, December 25, 2014

Thoughts on the scientific method (IV): string theory

This post (sorry for the delay) is the concluding part of a four-part series, the first three parts can be found here, here and here.

To summarise the main points that I argued previously: (i) logical positivism and the criterion of falsifiability are not necessarily appropriate guides to how science should be practised, (ii) the word "theory" is inconsistently used and best avoided in such a discussion. What science does, in practice, is to pursue goals, develop frameworks and formulate models. In applying criteria like testability, verifiability and falsifiability, one needs to keep this classification in mind, (iii) Quantum Field Theory (QFT) is the framework used to describe fundamental particles and forces. Quantum Electrodynamics (QED) and Quantum Chromodynamics (QCD) are two distinct (but similar in some ways) models formulated to describe the electromagnetic and strong interactions in nature, and both have been extremely successful when confronted with experiment (QED is the unique model in all of science that produces predictions from first principles in agreement with experiment to an accuracy of nine decimal places).

I also pointed out that Classical Mechanics is already "falsified" since it cannot explain a large class of phenomena -- precisely those phenomena which we refer to today as "quantum" or "relativistic". To explain such phenomena we need to invoke Quantum Mechanics and/or Special Relativity. However, I argued that frameworks should not be thought of as falsified even when they have been contradicted by experiments. Classical Mechanics is still taught as a subject in school and college for a very good reason: it is a very successful framework. We understand that it is successful in the domain where it should be applied, namely the domain where it works! Such reasoning may appear circular but is, quite rightly, accepted and followed in science. It is questionable only if you insist on a literal application of logical positivism and falsifiability.

QFT is a difficult framework and a large fraction of physicists remain unfamiliar with its depths. Perhaps for this reason, it is not widely realised that QFT has also beem falsified, by the experimental fact that gravity exists. QFT with gravity is not "UV complete" and this means it will inevitably break down at very high energies. A number of physicists believe we should not worry about this until we are able to perform measurements at those energies. And we may have remained in this mode but for a fortuitous accident. A model (not framework) had been proposed by Nambu, Susskind and Nielsen to qualitatively describe the binding of quarks in a proton, which has a strange property: the force between quarks is stronger at large distances and weaker at short distances. One (perhaps the only) place where we encounter this in classical physics is the behaviour of a rubber band. So the above scientists (one of whom now has a Nobel prize, though not for this idea) proposed that quarks behave as if they are connected by rubber bands. The formalism to describe this is string theory. Thus, much as in the case of QED, a model led to the development of a framework.

As has happened many times before in physics, string theory began to emerge as a framework that could encompass far more than was originally imagined. From its initial role as a model for quark interactions it grew to provide a consistent framework of quantum gravity, satisfying the very criterion ("UV completeness") that the framework of QFT failed to satisfy. The framework is able to naturally accommodate other "gauge forces" and a bold proposal was made in 1984 that one may be able to find a "theory of everything", a unified model of all fundamental forces including gravity, within the string framework. This proposal may be right or wrong, we don't have much guidance today - neither from experiment nor from theory. There is no compelling model (though models with specific compelling features exist) and no positive experimental result (such as proton decay). And indeed, work on this proposal has been scaled down considerably since the early days.

Through the above developments, a framework emerged which reduces to ordinary QFT in the limit of small strings (exactly as quantum mechanics reduces to classical mechanics in the limit of small quantum effects). It is a very powerful framework that addresses a wide variety of topics in theoretical physics. Indeed, a string theorist today is not someone who necessarily does string theory, but someone who has expertise with the framework and is able to use it wherever needed. In the last ten days alone, I have attended talks on topics ranging from quantum phase transitions in superconductors, to black hole physics, to fluid dynamics, to quantum entanglement, to cosmological inflation. But during all this time I was only at "string theory" conferences, and the speakers were all "string theorists". Many of the talks made no mention of string theory but the theoretical techniques were, sometimes very dimly, related to string theory. The goals in these conferences were not connected to the unification of fundamental forces - a goal that will be revived if and when there is a strong new motivation either from theory or experiment - but rather, to a wide variety of physics goals. The topics listed above are firmly rooted in empirical reality, but theoretical work (without string inspiration) has often been too limited in its ability to provide an understanding of them.

Skepticism is integral to science. But skepticism does not mean that one points to, say, the special theory of relativity and says "I don't like it" (as many people did in the time of Einstein). You may not like it, but you need to present something as good or better and defend that scientifically. In the medium to long term, frameworks or models that are not compelling and serve no useful purpose simply fade out. They do not get stamped out by someone writing an article in Nature whose title is a call to arms and which casually tries to push an unpopular competing theory due to one of the authors.

I'll conclude by providing three possible developments which could easily be around the corner and which would force even skeptics to sit up: (i) the discovery of supersymmetry - this would be an entirely new corner of physics that arises most naturally from string theory, (ii) the discovery of a controlled model of quark confinement within string theory, (iii) the discovery of a tensor-scalar ratio r greater than, say, 0.01 in the cosmic microwave background. If you are interested in physics but don't know about one or more of these topics I suggest you read about them, because they are important.

And if you are a physicist, the question you should be asking is: can I learn something from string theory about the scientific goals important to me?

Saturday, December 20, 2014

Thoughts on the scientific method (III): quantum fields and particles

Note: The first two parts of this multi-part article can be found here and here.

Several theoretical frameworks have played an important role in physics. Classical mechanics, quantum mechanics and statistical mechanics are all frameworks. It is worth repeating here that in and of themselves, none of these make direct predictions that can be "tested" or "falsified". For example in classical mechanics one can write down the Hamiltonian of a hypothetical system and study the solutions of this problem, even if such a system has no existence in nature. We do this all the time: problem sets in textbooks are aimed to teach us how to use classical mechanics and not always how to make definite experimental predictions.

It is then up to us to make a model of a chosen physical system and try to experimentally test that model. If the model has been designed with suitable hindsight, it will surely work qualitatively up to a point. But now we test it by going to higher accuracy or varying the experimental parameters. What if the model fails, i.e. it disagrees with experiment? Then there are two very different possibilities: (i) the model failed because it was inadequate as a model and can be improved by tweaking it, for example by adding another term to the Hamiltonian,  (ii) the model failed because classical mechanics as a framework is inadequate to address the problem. Both these types of failures are well-known and well-understood. In category (i) falls virtually any concrete model, for example a model of fluid dynamics that is missing some important feature of the fluid under study. One then rectifies the model by adding a term that captures this feature. In category (ii) is the fact that the electron in a hydrogen atom simply cannot be described by any known Hamiltonian in classical mechanics. One might say the framework of classical mechanics is thereby falsified and replaced by quantum mechanics. But I prefer to think that frameworks are not falsified. They simply outlive their usefulness and applicability.

The appropriate framework to describe elementary particles and fundamental forces is quantum field theory (QFT). It encapsulates both classical and quantum mechanics and extends them to the relativistic domain. By considering finite-temperature field theory, one also encapsulates statistical mechanics. This framework was originally formulated by Feynman, Schwinger and Tomonaga to study the quantum theory of electromagnetism. QFT is difficult and takes years of study to master. But merely mastering how QFT works would not provide us any description of electromagnetism: one needs an actual model within the framework of QFT. This model, called "quantum electrodynamics" (QED) was proposed by the above authors and has been a spectacular success. It is noteworthy that historically, the study of QFT (the framework) and QED (the model) went hand in hand.

Interestingly, QFT also has applications to condensed matter physics. It can be reformulated to describe a many-body system such as a crystal with local interactions between different sites. The framework is (essentially) the same but the physical models one studies are quite different, bearing little resemblance to QED. The models are tailored to study some material of interest, rather than the interactions of electrons and photons in the vacuum. It is remarkable, but no longer surprising to any experienced physicist, that a framework created to deal with one class of systems can be usefully applied to very different classes of systems. In the previous posting I referred to the "renormalisation group" which was also an example of such a framework, indeed it is a part of the overarching framework of QFT.

The fact that one framework can apply to very different systems has played a central role in the development of physics. Perhaps the best example is that of the mass problem for weak vector bosons. Such bosons were proposed by Schwinger in the late 1950's as mediators of the weak interactions. By the early 1960's, many physicists were looking for a mechanism to assign a mass to such particles without contradicting the requirement of gauge invariance, a crucial consistency condition for vector bosons in QFT. A possible mechanism was first suggested in 1963 by Phil Anderson using an analogy with the properties of superconducting materials. These embryonic ideas were converted in 1964 by Englert and Brout, and Higgs, into a mechanism that can be generically applied to elementary particles: the Higgs mechanism.

As I've already mentioned, there was at first no definite prediction of how the Higgs mechanism should be tested, and no definite model - just a mechanism within a framework. But by the end of the 1970's, using both the Higgs mechanism and a novel framework due to Yang and Mills dating back to 1954, a single unified model of the electromagnetic and weak interactions was achieved. It is often called the "electroweak" model because it unifies electromagnetism and weak interactions in much the same way as special relativity unified electricity and magnetism at the beginning of the 20th century. The electroweak model had many predictions, some of which (the existence of W and Z bosons) were soon tested, at first indirectly and then directly. Other predictions like the Higgs boson had to wait 50 years.

In the meanwhile a model of the strong interactions (QCD) was proposed in 1973. The authors of this theory were very clever, but they also had a lot of good fortune. The frameworks of QFT, including Yang-Mills theory and the renormalisation group, were available. Experiments indicated the existence of quarks that interacted weakly at short distances. They proposed QCD by putting together all these ingredients in a brilliant and elegant fashion. I must mention here that if the Yang-Mills framework had not been (i) known, (ii) rendered respectable by its success in a totally different system, the weak interactions, (iii) rendered consistent by the mathematical work of 'tHooft and Veltman, the strong interactions would have remained a mystery. But none of these points (i), (ii) and (iii) have anything to do with experiments on strongly interacting particles.

QCD together with the electroweak theory forms what is today called the Standard Model of fundamental interactions. This describes all elementary particles in nature and all the fundamental interactions among them, except gravity, and it is a stunning success at extremely high levels of precision. Such an ambitious enterprise was surely not anticipated by Feynman et al when they initially formulated QFT. However, if they had been different people, or the age had been different, they might have ambitiously declaimed in 1948 that the QFT framework would come to describe all the fundamental forces relevant for terrestrial particle physics - a "theory of everything". For saying this they would have surely been ridiculed, but they would have been correct.

(to be concluded)

Friday, December 19, 2014

Thoughts about the scientific method (II): goals, models and frameworks

Note: This is part (II). Part (I) can be found here.

One of the most confusing words in philosophical discussions of science is the word "theory". The general public usually does not know what this means, and even within the physics community there is no widespread agreement on its meaning. Compare the following phrases: quantum theory, density functional theory, Fermi liquid theory, BCS theory, big bang theory, theory of elasticity, gauge theory, quantum field theory. Any physicist would agree that the word "theory" is being used here with very different meanings. This makes the question of whether a given "theory" should be testable, or falsifiable, extremely muddy.

I will try my best to shine a little light into the mud (though I cannot guarantee the transmission or reflection of such light!). Let's consider three words that are related to "theory" but have more unambiguous meanings: goal, model, framework.

A goal, clearly, is something that one would like to understand. Some possible goals in Physics are "superconductivity", "nanomechanics", "molecular motors", "quark-gluon plasma", "photonics", and "quantum gravity". These are sometimes phrased as theories, e.g. "theory of superconductivity" but as this example shows, such phrases are very unclear and it's better to think of them as goals. One advantage of focusing on goals is that each one typically has an experimental and a theoretical side: for example an experimentalist may study quark-gluon plasma at an accelerator while a theorist could formulate a model to describe the transport properties of this curious state of matter. However, very often there is no symmetry between the experimental and theoretical sides. For example, photonics is largely an experimental effort to transmit, modulate, amplify and detect light. The theoretical basis for light-matter interactions, known as quantum electrodynamics, is very well known and verified, and one does not aim to test or improve it using photonics (but there is still room for theorists to work out the properties of light in specific media). The important point is that photonics is driven by its potential application in telecommunications, medicine, metrology and aviation, to name a few areas. As such, it is more experiment-driven than theory-driven.

Now let's move on to models. Some useful examples are the "nuclear shell model", "Hubbard model", "Yukawa model" and "dual resonance model". Each of these models is a specific attempt to understand particular physical phenomena. Respectively, the above models try to understand: the energy spectra of nuclei, the metal-insulator transition, the nature of strong interactions, and resonances in high energy scattering. In each case the model is rather precisely aimed at a goal and is somewhat successful in describing the system in question. Also, in each of these cases the model has obvious limitations: the shell model fails to explain multipole moments of nuclei, while the Yukawa model does not provide accurate numbers for scattering amplitudes. In fact, all the above models are "wrong", in the sense that they are all contradicted by definite experimental measurements. In some cases they have been superseded by better models that also do not work completely. For example the shell model was replaced by the collective model that won a Nobel prize in 1975 for Bohr, Mottelson and Rainwater, but it too has had limited success. Inspite of this, the models I've listed are all useful and continue to be used by scientists for various purposes. It is important to understand that though they were contradicted by specific experiments, the models were not thrown out.

I expect a layperson will be  surprised to learn that physicists use models that actually disagree with some experiments. On the other hand, physicists are aware that scientific models can have limited applicability. Though we routinely accept this, I sometimes wonder how honest we are being. It's not that we always decide in advance which model needs to apply to a given situation, rather we often test a theoretical model against experiment, find that it doesn't work, and then - instead of saying "oh this model is wrong" - we say it is not applicable to that experimental situation for some reason. In other words, the model works only when it works. This is not a perfect way to do things, but it's what we can do, and we are all used to doing it.

Finally some words about frameworks. These are less familiar to the general public than goals and models, because they are usually technical, even though they can embody profound physical concepts. A framework is not a model of a system, but a way of thinking about large classes of systems. A very beautiful example, familiar to physicists across many (but not all) areas, is the renormalisation group. This teaches us how to follow the evolution of any microscopic system over a change in the effective length scale. It introduces the notion of "fixed point", a universal behaviour to which a wide class of systems converges. This work originated in particle physics in 1954 and was developed by Kadanoff and then Ken Wilson (who got the 1982 Nobel prize) in the 1960's and 70's in the context of statistical systems. Wikipedia tells us:
 "The renormalization group was initially devised in particle physics, but nowadays its applications extend to solid-state physics, fluid mechanics, cosmology and even nanotechnology.
There is a profound lesson here. A framework like the renormalisation group, on its own, does not make any predictions about any system. It doesn't even know what system we are talking about! In order to be converted into a testable idea it has to be incorporated into a model. When it was proposed in 1954, quarks had never been thought of and quantum chromodynamics  did not exist. However, when experimental circumstances prompted the possibility of a theory of quarks, the notion of renormalisation group was already around and could quickly be incorporated into the seminal work that won Gross, Politzer and Wilczek a Nobel prize in 2004.

Thus a framework is a theoretical concept built out of past experience in physical reality, that takes the theoretical understanding to a higher level and can then be applied in various contexts to situations that may not even have been anticipated during the original development. For example the 1954 work on the renormalisation group was developed for, and applied to, quantum electrodynamics, but had this enterprise failed to be tested, the framework would still have been lying around waiting for its applications to yield the 1982 and 2004 Nobel prizes. From the standpoint of theory, frameworks are incredibly valuable things, often more valuable and durable than models.

(to be continued)

Thursday, December 18, 2014

Thoughts about the scientific method (I)

After a long time away from this blog, I felt compelled to return to it. The proximate reason is a recent article in Nature about what does - and does not - constitute science. But I'll first introduce the topic and make some comments on it, then get to the article in a subsequent posting.

The issue at hand is "what is the scientific method?" and "what constitutes science?" (as opposed to pseudo-science or non-science). This keeps popping up for a variety of reasons. On one side, there are schools of thought that would like astrology to be included with science. This worries many (not all) scientists. On the other, there is a concern that some branches of science as currently practiced are "not scientific". This also worries some (not all) scientists. In both cases, the empirical method and the concepts of testability and falsifiability are produced to justify the arguments made. My concern is that there is not enough reflection on what this method and these words really mean, and I would like to put forward some thoughts on this.

Let me start by quoting from a popular article I wrote for the Times of India  about seven years ago:

The notion that scientific theories must be tested experimentally is fundamental to the doctrine of positivism, which also requires that theories must always deal with quantities that are observable. [...] But Steven Weinberg, a Nobel Laureate and one of the greatest living physicists, asserts that "positivism has done as much harm as good". To make this point, which he develops at length in his excellent book "Dreams of a Final Theory", he argues that it was positivism that kept a number of scientists from believing in atoms, in electrons and much later in quarks.

Weinberg supports his claim with a comparison of two scientists. The British physicist J.J. Thomson is credited with the discovery of the electron, but Walter Kaufman in Germany performed the same experiment independently at the same time, and even managed a more precise measurement of the electron's properties. While Thomson reported the discovery of a new particle, which he named the electron, Kaufman merely reported the phenomenon he had observed (the bending of cathode rays). Exercising a positivist's restraint, he did not assume it corresponded to a new particle. [...] The harm caused by a positivist approach, in Weinberg's view, is this: unless one is willing to make - and believe - a hypothesis based on the limited information available, there tends to be a lack of direction in one's subsequent research. Only if one makes a conjecture about what is happening, defying positivism at least temporarily, is one motivated to perform experiments that can confirm or deny the conjecture.
The physicists I know routinely claim to be positivists. However, when confronted with the above argument, which contradicts their point of view, they instantly agree with it. I don't mean to only criticise others: I'm an early example of this phenomenon. In 1998 I attended a workshop in Santa Barbara where Stephen Hawking gave an informal talk to a round table of around a dozen people. He started by saying he was a logical positivist and then added "this is also how most physicists would describe themselves, if only they knew what it means". I was in awe of Hawking and was seeing him for the first time. So it never crossed my mind that he could be talking through his hat, but now I'm pretty sure this was the case.

This is not to say that I disrespect the spirit of positivism. Experiment and experimental verification are fundamental parts of science. The problem arises, just as in the example above, when one forgets some key factors: (i) the complexity of the interplay between theory and experiment, (ii) the presence of (sometimes long) periods where one or the other of these has to surge forward without any support from the other, (iii) the role of intuition, guesswork and leaps of faith in temporarily furthering the cause of science.

To explain point (i): there is no simple mechanical routine where someone does an experiment, then someone writes a theory to explain it and predicts a new experiment, then another experiment is done etc. The interplay is complicated and often incomprehensible to both theorists and experimentalists at the time they are working. This is why every great scientist confesses in her retirement speech that she didn't really understand what was going on while she was making great discoveries.

On point (ii), there are periods in science when theory is stuck for lack of ideas or computational tools, or experiment is stuck for lack of ideas or experimental equipment. At present there is little theoretical understanding of "dark matter" but experiment must continue until the theorists catch up. Conversely there is little experimental understanding of "quantum gravity", so theorists must do their work and wait until experimental understanding is achieved.

Finally about point (iii), the word "temporarily" is crucial. A fundamentalist who blindly follows positivist ideology might not be able to do what everyone in science routinely does: mull over a hypothesis at night and resolve to test it the next morning. Just 12 hours of speculation might, in his overly pedantic view, be considered non-positivist! Of course, no scientist would consider such speculation wrong or unscientific. But if it's OK to speculate overnight, is it OK to do so over a month, a year or a decade? And this is a very crucial point. The scientists who designed and built the Large Hadron Collider relied on theoretical speculations from 1964 about the existence of a Higgs boson (this is why the experiment was optimised to find this boson, and found it nearly half a century later). Do we consider fifty years of speculation about the Higgs to be unscientific? I think not.

I know the standard response to this line of argument: "The Higgs speculation was focused on creating an experimental test. If the Higgs were eventually found it would validate the speculation, while if it were not then the speculation would have been falsified. Thus the entire process followed Karl Popper's criterion of "falsifiability" and is therefore admissible as science."

I disagree on two counts. The Higgs hypothesis was not initially focused on an experimental test. Englert-Brout and Higgs did not suggest any experimentally verifiable picture of their idea in 1964. It took many years of theoretical research to arrive at the possibilities and predictions that were lined up by the time the LHC started to operate. So the fifty years until verification were not merely due to experimental limitations. There were theoretical issues that needed to be understood, in a speculative (i.e no Higgs particle was known to exist) but totally scientific context.

My second disagreement though is more significant. I simply don't agree with Popper's falsifiability criterion. It sounds nice the first time you hear it. However - like all the lapsed positivists described above - you may change your mind when you consider its implications.

Continued.... Click here for the next part.