Has Quantitative Finance reached its limits? I intend to answer this from a principled point of view, in the same spirit as someone might answer the question “Has biology or physics or literature reached its limits?” Of course there is always more work to do, but is there something drastically new awaiting us?
I don’t want to be like the famous scientist in 1899 who said we’re at the limits of our knowledge of physics, doomed to simply working out progressively higher order perturbation expansions of known theories, only to then be upstaged by the discovery of quantum mechanics and relativity a few years later. But nevertheless, I do feel that quantitative finance has become a bit too mechanical, a repetitive turning of the handle.
Perhaps too much of quantitative finance has become focused on the engineering aspects of the field. When I first heard the words “financial engineering” about twelve years ago, I thought they were a poor description of our field. I thought of what I and my colleagues were doing as science.
Mechanical engineering is concerned with building devices based on the principles of mechanics, i.e. Newton’s laws, suitably combined with empirical rules about the behavior of more complex forces (friction, for example) that are too difficult to derive from first principles. Electrical engineering is the study of how to create useful electrical devices based on Maxwell’s equations of electrodynamics. Bio-engineering is the art of building prosthetics and other biologically active devices based on the principles of biochemistry, physiology and molecular biology.
Engineering is constructive – you use the principles you know to build what you need. Science,– mechanics, electrodynamics, molecular biology, etc. – is usually reductive and seeks to discover the fundamental principles that describe the world.
What about quantitative finance? In a perfect world, financial engineering, layered above a solid base of financial science, would be the study of how to create functional financial devices – convertible bonds, warrants, default swaps, etc. – that perform in desired ways, not just at their expiration, but throughout their lifetime. The original method of doing this was static replication, understood for decades. Then Professor Merton and his co-discoverers discovered dynamic replication and showed us how to construct the new financial devices the world craved. Dynamic replication is.based on the approximate science of Brownian motion, and idealization that, while it captures some of the essential features of asset price uncertainty, is not ultimately a very accurate description of the characteristics of the process.
Further fundamental progress in quantitative finance is dependent on advances in financial science, the study of the fundamental laws of financial objects, be they stocks, interest rates, or whatever else your theory uses as atomic constituents.
Can we do better? We are certainly rich in technique (stochastic calculus, optimization, the Hamilton-Jacobi-Bellman equation, and so on), but we need the right laws to which to apply these techniques. Too much of quantitative finance is often the application of familiar techniques to new situations and securities.
There’s not doubt we’re very good at derivatives pricing, the technique of very sophisticated interpolation which allows us to move from the known prices of liquid securities to the unknown prices of illiquid ones that depend on them.
How well does this work? Dynamic replication isn’t quite as accurate as it sounds; it’s partly an illusion; you can’t hedge as perfectly as Black-Scholes implies, because markets jump, volatility is stochastic, and you can’t hedge continuously, to name just a few of the most obvious reasons. Dynamic hedging is much harder and less accurate than most textbooks lead you to believe, and the practise of hedging drags you unavoidably into the messy business of building complex systems, data entry screens and databases. If traders had to genuinely make their money by theperfect replication of each option, they’d have a tough time.
There are more sinister illusions than dynamic replication. One is the belief that somewhere out there is a perfect scientific model that, if you just supply with the right numbers, will produce the right price. But our models hardly ever produce more than the most approximate truth in finance, because “true” financial value is itself somewhat of an illusion. In physics, a model is right when it correctly predicts the future trajectories of planets or the existence and properties of previously unobserved particles. In finance, you cannot easily prove a model right by such observations. Data are scarce, and, more importantly, markets are arenas of action and reaction, dialectics of thesis, antithesis and synthesis. People learn from past mistakes and go on to make new ones. What’s right in one regime is wrong in the next.
As a result, practitioners don’t expect too much from a model. The soon learn that models are tools for thinking about things, not calculators for generating incontrovertible numbers.
So, for me, the next big step will be a scientific one: a better theory of underlyers, not derivatives. Markets are collective phenomena, and the great advances in dealing with collective phenomena in thermodynamics and statistical mechanics in the late 19th Century came from linking the observable macroscopic to the unobservable microscopic – deriving the known laws of thermodynamics and matter from the statistical behavior of atoms and molecules.
To do that, you first have to know the macroscopic laws. Over the past few years, Gene Stanley at Boston University and his collaborators seem to have discovered some fascinating near-universal power laws for the tails of stock price distributions, trading volume and trading frequency. They’ve then tried to explain on a more microscopic level how these power laws can arise from the empirical distribution of the sizes of financial firms and these firms they break up their large trades to minimize market impact. I don’t know if these models are right, but to me they aim in the right direction, trying to rationalize what we observe on a large scale with hypotheses about the behavior or market participants.
Can such models be stationary, like true scientific models of the natural world, or will our knowledge of these models alter them as we use them? If so, we’re in for an infinite regress. But in any event, if I could chose to come back in fifty years and ask a question about finance, I’d ask whether people understand underlyers better, not derivatives.