Why String Theory?

by Joseph Conlon

  This style of work is essential for progress in physics. The aim of these calculations is in general not directly the discovery of new physics – no one computation is done with the expectation that it will lead to a breakdown in the Standard Model. However, any such result may end up as the key element in a discovery. A minute, but established, deviation from expectation can be the herald of great change. For example, it was the anomalous advance in the perihelion of the planet Mercury, at a rate of one-hundredth of one degree per century, that was the first harbinger of general relativity.

  Something similar may in time be true for the Standard Model. For example, one of the four main experiments at the LHC is called LHC-B. It is designed to study the production and decay of particles involving the bottom quark. One way the bottom quark can join with other particles is to produce what are called B-mesons, consisting of a bottom quark and an antiquark. These B-mesons live for a short period of time and then decay. Among other goals, the LHC-B experiment aims to measure precisely the rate at which these B-mesons decay and the different types of particles they decay to.

  Of particular interest are so-called ‘rare decays’ – processes that the Standard Model predicts will happen maybe only one time in a billion. If such a B-meson were found to decay in this manner even as much as once in a hundred million times, it would be an unambiguous signal that the Standard Model is wrong – a signal as unambiguous as if a new heavy particle were to be discovered directly and spectacularly. If this occurs – and while it has not happened yet, it could – it would only be because of long and careful calculations of exactly what the Standard Model predicted.

  You will however find such calculations only rarely featured in the pages of New Scientist or Scientific American. Let it not be said that this has gone entirely unnoticed, or that those who work on the predictions of known theories ever feel a tinge of satisfaction at an absence of signals for new, speculative and well-hyped ideas. Let it not be said that schadenfreude is ever felt when such ideas fail, or that the trendy set’s dismissal of precise calculations as ‘German physics’ could ever contribute to this emotion. Let it not be said, because of course it is not true.

  I have chosen to illustrate this style of physics using the example of precision calculations within the Standard Model. However, it is not confined to this topic. Many areas – certainly including string theory – have definite frameworks, in which well-defined but difficult calculations can be carried out, leading to well-defined results. Examples in string theory are tests of the AdS/CFT or gauge/gravity correspondence, which I touched on in chapter 8. These tests involve difficult but precise computations in quantum field theory that are directly analogous to the next-to-leading-order or next-to-next-to-leading-order computations in the Standard Model. Over the almost two decades since the AdS/CFT correspondence was first formulated, these tests have become progressively more intricate and complex.

  It is a very human choice to follow paths of clear scientific value even if the act of doing so may exclude the absolute highest levels of achievements. It may perhaps be compared to choosing to be an accountant rather than a dotcom entrepreneur. Both business and science need those who will risk everything, and those who prefer definite but limited return over a small chance of glory.

  12.3 STOCKHOLM OR BUST

  As we have also seen, the Standard Model is, in matters empirical, conceptual and practical, the very model of a modern scientific theory. It works. It is deep. It correctly predicts the results of a dazzling range of experiments to an enormous level of precision. However, every particle physicist also knows that the Standard Model is incomplete. It is not a full theory of nature. Every particle physicist knows that, at some energy scale, new particles and new interactions will appear. They know that there is a new theory, which lies beyond the Standard Model but encompasses it, and which is true in the deepest and most wonderful sense of that word. That theory is out there, waiting to be found, in the same way that still untouched hoards of Roman and Saxon gold lie in country fields waiting for the farmer’s plough. They also know that glory is reserved for the first person to write that theory down.

  This section is about model builders, those who propose ideas for new physics beyond the Standard Model that can then be tested experimentally. This sober description does little justice to the reality. There is a traditional story, popular in textbooks, of how progress in physics occurs. Those outside science like to call this story the scientific method, and it goes like this. Alice is a theorist. She thinks hard and invents a new theory about nature. Alice is aware of the results of existing experiments, and she checks that the new theory is consistent with the existing data. Alice then works out the predictions of the theory for measurements yet to be performed. Bob is an experimentalist. Bob looks at the predictions of Alice’s theory. He thinks about what these predictions mean and builds an experiment to test them. He carries out the experiment and analyses the results. Do the results agree with the predictions that Alice made? If yes, bully for Alice. If not, her theory is wrong, another false idea is discarded and the great engine of Science steams on.

  This is the theory of scientific progress, and in theory it should coincide with the practice. In practice, it does not. To succeed, this approach requires cheap experiments and a surplus of data compared to theories. However in the world we live in, ideas are quick and cheap but experiments are long and expensive. This can be seen by looking at the electronic paper repository arXiv.org. The arXiv – as it is known – has revolutionised scientific publication since its inception in 1992. Every weekday, fifteen or so papers are uploaded to the phenomenology section of the arXiv preprint server, the section concerned with theories that may explain data. If we take twenty pages as the typical length of a paper, this corresponds to the uploading of one medium-size book a day. Discounting weekends, fifteen papers a day adds up to three hundred papers per month. Even if simply one paper in every ten of these involved proposals for models of New Physics – and regular readers know the true fraction is higher – that still makes one such proposal a day, a rate far in excess of the build time of experiments.

  Any scientist who proposes the existence of a new particle or a new force of nature is one dreaming of a big discovery. They are hoping, with a fortunate roll of the dice, to be in the right place at the right time and with the right idea. Unlike the would-be revolutionaries, they are not seeking to overturn the entire structure of physics. It is sufficient for them to be right once. It is somewhat analogous to the footballing phenomenon of the goalhanger, the player who always waits around the opposition’s goal, hoping for the chance to stick the ball in the net.

  The fact that the stated aim of model building is to make a prediction of new physics, and to see it confirmed by experiment, has an important corollary. Particle physics experiments take a long time to build, and the backdrop for this book is the fact that over the last forty years the Standard Model has been enormously successful at describing nature. The sad but sober truth is that over this period no evidence for any physics additional to the Standard Model has emerged. This statement can be glossed in various ways, and various small exceptions urged – what about neutrino masses? What about dark energy? What about inflation? While these points can be debated, it is not up for debate that the large accelerator complexes have provided fantastic confirmations of the Standard Model but no signs yet of any new physics beyond it.

  It is striking that this history has in no way prevented many physicists from building careers – indeed, from building highly successful careers – through putting forward ideas for new physics beyond the Standard Model. Not a single one of these new model-building ideas put forward since 1974 has ever succeeded. This does not prevent the originators of these ideas receiving some of the highest accolades in science, as well as the largest financial rewards available.6

  In terms of actually predicting novel experimental phenomena, then, none of these models have been successful. What does make a mod
el successful? From a worldly perspective, a model is successful if lots of attention is paid to it. When this happens, postdoctoral researchers will add epicycles to it, while experimenters will make dedicated searches to look for its features and place limits on its parameters. Graduate students will develop further modifications, and write PhD theses explaining how the aforementioned experimental limits can be evaded by removing the twelfth epicycle and adding a sixteenth one. Large numbers of papers will cite the original incarnation of the model, thereby reconfirming the importance and significance of the original paper. As the absence of any positive evidence accumulates, models sublimate into infinitely flexible paradigms that can never be excluded and can accommodate any observation.

  The scale of this can be impressive – although to be fair, one should not blame the original authors for the subsequent take-up of an idea. As an illustration, the four original papers of two popular models – the so-called Large Extra Dimensions and Randall-Sundrum scenarios – have around 5500, 3800, 6800 and 5500 citations respectively. These are enormous numbers for phenomenological ideas with zero experimental support.7 Such models can rarely if ever be totally ruled out, as there is always some wiggle room for playing with parameters and tweaking terms so as to avoid any given experimental constraint. As models evolve into industries, pointing out the absence of any favourable experimental evidence becomes unseemly: a bit like commenting on the Emperor’s willy rather than on the magnificence of his clothing.

  To become a successful model builder, it is then not a requirement that the models actually describe nature. The overabundance of models compared to data has an additional effect on the language used in papers. As models need attention like humans need oxygen, the consequence is adjectival inflation. Models are natural, explanations are elegant, and conclusions are compelling. For the prospective model builder, salesmanship is a not unuseful skill to have.

  In principle, all of the above makes zero difference. Science is driven by experiment. Over time, truth will out. Inflated claims are exposed, and nature, not us, will determine the correct explanation. Indeed, the Standard Model itself was in part built according to the above method. Claims were made, ideas were proposed – and data eventually singled out the ideas that were correct and dissolved inappropriate hyperbole. In the end, the models that are correct survive and flourish, while those that are wrong are winnowed away to the aether as chaff.

  This is indeed all true – in the long run. In the long run, we are also dead. While the long run may be characterised by eternal verities, the short run is what determines the quotidian mundanities of jobs and salaries that can afford a mortgage. Flattery may not soothe the dull cold ear of death, but it is pleasing enough to the living.

  12.4 THE MOST SUBLIME BRAHMINATE OF PRINCETON

  Theoretical physics is a deep subject that concerns itself with big questions. As we have seen in this book, some of these questions are very big indeed and lie at the heart of quantum gravity. What is the fundamental physics of black holes? What is the nature of space and time? What is physics like at energies near the Planck scale? What is M-theory? These questions are hard, with no answers that can fit into a one-hundred-and-forty-character tweet. As we have also seen throughout this book, there will be no quick experimental solution. The ugly detritus of proton collisions at the Large Hadron Collider will not tell us about physics at distance scales smaller by a factor of ten to the fifteen than those that can be probed at CERN. How can these questions then be answered?

  The history of western philosophy is glibly observed to be a history of commentaries on Plato and Aristotle. Plato and his student Aristotle were two of the greatest philosophers of the ancient world, but their approaches to philosophy are marked by two distinct styles. Roughly, Plato saw objects in the world as approximations to ideal objects, called Forms. When I use a pen to draw a circle on a sheet of paper, it is not a perfect circle. My hand shakes slightly and is not perfectly steady as it draws. The line has a finite width. Nonetheless, you can recognise that what I am trying to draw is a circle, and we can conceive of the notion of a perfect circle even though no such perfect circle has ever been drawn. According to Plato, the perfect circle exists as a Form, and the actual circle I draw participates in this Form. These Forms – the idealisations of actual objects – play a central part in Plato’s philosophy. We are instructed to look beyond the imperfect reality of the pencil drawing of a circle on a page, to the Form of the perfect circle, of which we can conceive despite never having seen an explicit example. The focus of study is not the actual circle on the actual page, but the Form to which the drawing alludes.

  With Aristotle, the focus is reversed. Aristotle was not a scientist’ – the word was not even coined until 1834. He was however inordinately curious about the details of the natural world and interested in the haecceity – the thisness – of objects. Aristotle wrote about physics and the mechanical motion of objects. What makes a body move? Why does it continue to move and then stop? He wrote about biology – what are the functions of plants and animals? What does the oesophagus do? These were not just abstract queries, but questions based on lengthy personal observation of animal and plant life in its many possible forms. He also wrote about astronomy, poetry, ethics and politics – while additionally functioning as personal tutor to the future Alexander the Great. One cannot help reflecting that at a dinner party he would have been either the most sparkling company or a consummate bore.

  The difference in style between Aristotle and Plato is roughly that while Plato saw an object as an imperfect version of a perfect Form, Aristotle saw the object in all its particular details: the hair of the cat, the teeth of the dog, the leaves of the tree. Seeing a snub nose, he did not extract an ideal property of ‘snubness’; the property does not exist without the nose. To Aristotle, the details were not mere accidental features of an object – in a certain sense, they were the object.

  The difference between the Platonic and Aristotelian approaches is the difference between those who want to remove inessential details to focus on the core properties of something, and those who see the details as the most revealing part. It is the difference between seeing the particular as an example of the general, and seeing the general as a collection of particulars. It is the difference in emphasis between loving humanity and loving your spouse. In particle physics, it is the difference between studying maximally symmetric super Yang-Mills theory and studying the actual strong force.

  The world needs both Platonists and Aristotelians, and so does theoretical physics. In physics the spiritus movens of the Platonists is located a short walk from the dormitory town of Princeton, New Jersey, at the Institute for Advanced Study. The Institute for Advanced Study was founded in 1930 as a pure research institute. It is located in a calm location, surrounded by woods and with deer running onto the Institute lawns. With an endowment of over five hundred million dollars, it is an iconic location for those who value research for the sake of research. Its members do not have to teach students or give lecture courses. They are instead free to pursue research on whatever topics they find interesting. The permanent faculty receive good salaries to live in comfortable homes in a beautiful environment, spending the rest of their lives thinking about whatever they wish – the Institute does not face difficulties in hiring. It is permanently associated with Albert Einstein, who joined as one of the founding faculty members when he was at the peak of his fame and attempting to construct a unified theory.

  In this attempt to construct a unified theory, Einstein was attempting to penetrate to the core of physics and to reveal its most basic principles. In his earlier discovery of general relativity, Einstein had done precisely this for space and time. Despite a level of experimental guidance that was somewhere between minimal and non-existent, he had been able to identify correctly the essence of the required theory and to write down the equations of general relativity. By obtaining a major result through the power of pure thought, Einstein became the exemplar o
f a theorist’s theorist.

  Einstein has now been dead for over half a century and physics since then has evolved dramatically. However his legacy, where the ideal result is one obtained without the need for experiment, persists. This style is characterised by a focus on clean problems, where the answers are well-defined and can be classified as either right or wrong. These problems do not have to be posed in the language of mathematics, but they should not be ambiguous, and formal elegance is appreciated in both the statement and the solution. The subjects addressed generally do not have direct empirical relevance; indeed, the question of relevance to observations can be seen as in slightly bad taste, betraying an overly vulgar interest in the quiddities of the world.

  This style is well suited to the classic theoretical problems that cannot be addressed experimentally. We have seen some of these problems within this book. An example is the question, discussed in chapters 3 and 11, of what the entropy of a black hole corresponds to. As was said then, the entropy of a black hole is a measure of the number of possible ways of rearranging the innards of a black hole, and black holes have been known to have an entropy ever since the work of Stephen Hawking and Jacob Bekenstein in 1973. However, what exactly are these different possible inner configurations? Once you know what they are, how do you count them? This question is perfectly suited to this style of physics. It is well posed. It has a clear answer. Experiment will not help you.

  In the context of string theory, this style is often associated with the attitude that the most pressing thing to do with string theory is to understand it. Applications come later: you cannot apply string theory until you first understand it, and the best way to understand string theory is in its own way and on its own terms. This means that the right calculations to do are those that reveal the inner world of the theory, often a world where there are ten dimensions of spacetime and a maximal amount of supersymmetry. Calculations, often with precisely chosen configurations of branes and in far more than three large spatial dimensions, are done to tease out subtle aspects of the theory.