The Pareto frontier approach to science

Creating new possibilities can be better than purely exploratory or purely practical research

One project I worked on involved collaborating with a bunch of organic chemists. One meeting, we spent an hour bouncing around ideas for crazy molecules we could make. Afterwards, my advisor (an engineering type) said with bemusement “this is what it’s like working with chemists, always focused on new chemistry, not on practical issues.”

There’s a common tension in science, between building for a specific application and experimenting just to see what happens. Funders often demand that a particular line of research has some practical application; supporting pie-in-the sky research is seen as too big of a risk. I get the sense that “just try it and see what happens” research is becoming less common over time.

But scientists often don’t know how their research will be used. Translating experiments into an actual product often takes decades, and the original researchers are unlikely to be involved. Whether a better solar cell makes it to market depends on a lot of unforeseeable contingencies like future raw materials costs, process automation details, and future competition. More fundamental research might find use in an entirely different product than the one people were expecting. This means that promising that a particular line of research will lead to a particular practical application is tenuous at best.

So I don’t think the chemists were wrong to approach research the way that they did. There are really two common approaches to science today:

The figure-of-merit approach. Here, we have a particular application in mind with a clear way to measure the utility of a particular solution. For instance, scientists studying solar cells might be interested in the percent conversion efficiency of their solar panels. A single metric is of overwhelming importance to the downstream application, so we can simply compare solar panels on that basis. The overall goal of the field is simply to maximize the figure of merit (perhaps on a cost basis). This is more common in fields that are closer to deployment.

The curiosity approach. Here, we just try stuff and see what happens. We might have a particular landscape that we want to explore, such as the lifecycle of a particular beetle species. Usually, the field is so far removed from practical applications that there’s no point of trying to measure or compare different solutions, such an idea might not even make sense in the context of the field. Instead, the goal of the field is to maximize knowledge about its area of focus.

But between these two extremes there’s a third way. Instead of squeezing every project into a particular application or consigning ourselves to purely curiosity-based exploration, we can conceive of the scientific process as a way to push frontiers. I call it the Pareto Frontier approach to science.

To see what I mean, take a look at this plot of volumetric energy density vs specific energy density:

Source

We see that hydrogen has the highest energy per kg, while aluminum has the highest energy per liter. These two elements form the Pareto front in energy storage. A scientist following the figure of merit approach might try to maximize volumetric energy density, searching for metals similar to aluminum that pack more energy per in a given volume. A purely curiosity-based exploration would have us measure the energy densities of a bunch of random substances so that we could learn more general trends.

But someone following the Pareto approach would ask: “can I invent a new substance that extends the Pareto frontier? One that has a unique, undominated combination of volumetric and specific energy density?”. On the plot, we would be looking for something that resides around (120, 70).

I think this is a better way of directing research effort. We often don’t know how knowledge is going to be used, and trying to predict it is hopeless. But if we create a solution that lies on the Pareto front for a lot of useful properties, we’re giving future inventors a new tool to work with.

This is more robust than the figure-of-merit approach, if the figure of merit turns out to be unimportant, we’ve wasted a lot of effort optimizing for the wrong thing. But solutions that lie on the Pareto fronteir are unique in a lot of ways increasing the liklihood that they’re useful for something.

Thinking in this way also helps us direct our curiosity more effectively. Consider the electrical and thermal conductivity of different materials. Some things like copper are good conductors of heat and electricity. Some, like plastic, do neither. Diamonds are interesting because they conduct heat very well but conduct electricity poorly. Lets plot these:

Looking at this, we’re immediately are struck with a new question: are there things that conduct electricity but not heat¹? It’s something I never thought to ask until this point (as it turns out, there are).

Mapping out the space of possibilities gives us new ideas about where to explore and directs our curiosity to places where learning more could be valuable. More than learning for learning’s sake, we should be learning about the limits of what is possible.

Pushing the volume of the Pareto frontier is a admirable goal for research². By extending the front, we not only enable practical applications we also get more knowledge of the space of possibilities. We no longer need to worry about whether a line of research is practical, or whether we’re exploring in the right place; if we push the domain of possibilities in a field, we’ve broadened the horizons of everyone who wants to build something with that knowledge.

1. This is hard in general, since electrons conduct heat.

2. It also suggests a way to measure the impact of a result, namely, how much a discovery increases the volume of the Pareto fronteir.