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QUANTUM gravity – the attempt to incorporate gravity into the quantum framework that describes the other forces of nature – seems an unlikely subject to spill out of physics conferences and become a passionate debate in the popular press. But string theory, the most popular approach to quantum gravity, has long been a darling of the science media and an intrigue in the public eye. That’s because the theory, in its original incarnation in the so-called first superstring revolution, claimed to be not only a way to quantise gravity but a complete Theory of Everything. From a framework in which both gravity and quantum particles are really strings vibrating in hidden dimensions, physicists dreamed that every aspect of particle physics would elegantly spill forth.

This idea, sadly, hasn’t panned out. What’s more, we have yet to find a conceivable experimental test of string theory. Nonetheless, there have been impressive advances on the theoretical front, including a second superstring revolution in the mid-90s. Among the most astonishing results was the discovery by Juan Maldacena that, in a particular space-time geometry, string theory is precisely equivalent to an ordinary quantum field theory living in a different number of dimensions. Results such as this convince string theorists that they are on the right track, even in the absence of experimental tests.

It has been a long time since the last revolution, though, and we are no closer to contact with real data. So perhaps it is not surprising that there is a backlash against string theory. Lee Smolin’s The Trouble With Physics is a paradigmatic example. Smolin is an excellent writer and a wide-ranging thinker, and his book is extremely readable. He adopts a more-in-sorrow-than-in-anger attitude toward string theory, claiming to appreciate its virtues while being very aware of its shortcomings. The Trouble with Physics offers a lucid introduction to general relativity, quantum mechanics and string theory itself, before moving on to a more judgmental critique of the current state of string theory and its future prospects.

While there is plenty to worry or complain about when it comes to string theory, Smolin’s concerns are not always compelling. For example, he finds it troubling that there are crucially important results in string theory for which rigorous mathematical proofs have not been found. But string theory isn’t alone in that predicament – there are almost no results about realistic quantum field theories that have been rigorously proven either. Physicists often take the attitude that reasonably strong arguments are enough to allow us to provisionally accept a claim, even in the absence of the kind of proof that would make a mathematician happy.

“String theory shows the triumph of risk takers pursuing their vision”

Smolin’s favorite alternative to string theory is loop quantum gravity, a theory that has grown out of attempts to quantise general relativity directly, without exotica such as supersymmetry or extra dimensions. To most field theorists this seems like a quixotic quest; general relativity is not well behaved at short distances and high energies, where other fields and particles are likely to play a crucial role.

Smolin argues that loop quantum gravity has an advantage over string theory in that it is “background independent”. This means that the equations that define the theory don’t refer to any particular geometry of space-time, as they do in special relativity, but apply equally to any allowed space-time, as in general relativity. Rather than picking some background space-time and studying the propagation of strings or other objects on top of it, the loop approach is formulated without reference to any fixed background.

But even if background independence is a good thing to have, it doesn’t follow that it needs to be put into a theory right from the start. This is an argument about the best way to construct a theory, not about the properties that theories should ultimately possess. Someday, if string theory turns out to be right, we will presumably be able to cast it in a background-independent form. In the meantime, string theorists are making progress by working in certain fixed backgrounds, and we should take progress where we can find it. It’s not an argument that anyone can definitively win until the right theory is found and we can look back to see which approach was more useful.

We do know that string theorists are winning the battle for support within the physics community. Faculty positions and grant money flow to string theorists much more than to anyone pursuing other approaches to quantum gravity. What’s really strange, though, is that there are any resources being spent on quantum gravity at all. If string theory were to suddenly fall out of favour, it seems much more likely that jobs and money would flow to particle phenomenology, astrophysics or other areas than to alternative approaches to quantum gravity.

Smolin talks a great deal about the need for physics, and academia more generally, to support plucky upstart ideas and scholars with the courage and vision to think big and go against the grain. This is a larger point than the specific argument about how to best quantise gravity, and ultimately far more persuasive; it is likely, unfortunately, to be lost amidst the noisy conflict between string theory and its discontents. The original dogged pursuit of string theory through the 1970s by Michael Green and John Schwarz is a perfect example of the ultimate triumph of risk takers pursuing their idiosyncratic visions, and Smolin is correct to lament the lack of support for this kind of research today.

In the real world, it’s difficult to see how to solve the problem. Faculty positions are extremely rare: within fundamental theory, a good-sized department might have two per decade, and it would be hard to convince a university to take a long-shot gamble for the greater good of the field. And a gamble it would be. Smolin stacks the deck by contrasting the “craftsmen” who toil within string theory to the “seers” who pursue alternatives, and it’s pretty obvious which is the more romantic role. Many physicists are more likely to see the distinction as one between “doers” and “dreamers”, or even (among our less politic colleagues) between “scientists” and “crackpots”.

To be clear, researchers working on loop quantum gravity and other non-stringy approaches to quantum gravity are not crackpots, but honest scientists tackling a difficult problem. Nevertheless, they have not managed to convince the rest of the community that their research programmes are worthy of substantial support. String theorists are made, not born. They are simply physicists who have decided that this is the best thing to work on right now, and if something better comes along they will likely switch to that.

Alternatively, if another decade passes without substantial progress, it’s not hard to imagine that string theorists will lose interest. I would bet against this possibility – string theory has proved to be a remarkably fruitful source of surprising new ideas, and there’s no reason to expect that track record to end.

Smolin is right in the abstract, that we should try to nurture a diversity of approaches to difficult questions in physics, even if his arguments concerning the specific example of string theory and its competitors are less compelling. He is also right that string theorists are not always as self-critical as they could be, and can occasionally be a mite arrogant. The best possible consequence of the appearance of The Trouble with Physics would be that physicists of all stripes are moved to take an honest look at the strengths and weaknesses of their own research programmes, and to maintain an open mind about nature’s ultimate verdict. Sometimes a little criticism can be a very healthy thing.