The Hubble Space Telescope’s famous 1995 Deep Field image captures galaxies in various stages of evolution. Many scientists have formulated and tested hypotheses based on Hubble observations. But the telescope itself was funded for reasons beyond evaluating a particular hypothesis. Credit: R. Williams (STScI), the Hubble Deep Field team, and NASA/ESA

“Not hypothesis driven.” With those words and a fatal grade of “Very Good,” a fellow reviewer on a funding agency panel consigned the proposal we were discussing to the wastebasket. I listened in dismay. Certainly the proposal had hypotheses, though it didn’t have boldface sentences beginning “We hypothesize . . .” as signposts for inattentive readers. Then I remembered the famous words from Isaac Newton’s Principia: Hypotheses non fingo. “I do not frame hypotheses.” If that approach worked for Newton, why do we have such a mania for hypothesis-driven research today?

The emphasis on hypothesis-driven research in proposals is strangely embedded in the scientific community, with no obvious origin in funding agencies. The word hypothesis appears nowhere in the NSF guide to writing and reviewing proposals, and only once in the National Institutes of Health proposal guide. Yet grant-writing experts universally stress that proposals should be built around hypotheses and warn that those not written this way risk rejection as “fishing expeditions.”

In recent years, a few voices in the biosciences community have questioned this exclusive focus on hypothesis-driven research, even as the mania spreads to the physical sciences. Allow me to add my voice. Evaluating grant proposals is hard, but shoehorning every proposal into the language of hypothesis testing benefits neither the prospective grantee nor the evaluator. It can also hinder scientific progress.

Hypothesis history

Isaac Newton, portrayed here in a 1717 portrait by Charles Jervas, wrote that he did not frame hypotheses.

Today many high school teachers present the scientific method as synonymous with hypothesis testing. Yet hypotheses are just ideas about how nature works, or what 19th-century scientist and philosopher William Whewell called “happy guesses.” Hypotheses organize our thinking about what might be true, based on what we’ve observed so far. If we have a guess about how nature works, we do experiments to test the guess. In quantitative sciences, the role of theory is to work out consequences of the guess in conjunction with things we know.

Perhaps the most famous hypothesis in all of science is that new species arise from the action of natural selection on random mutations. Charles Darwin based his hypothesis on observations of a few species during his famous voyage to the Galápagos. Charged with predictive power, Darwin’s hypothesis applies to all life, everywhere, at all times. Generations of biologists have tested and built on Darwin’s hypothesis with a vast array of new discoveries. The theory of evolution is now firmly established as the central pillar of biology, as well supported by evidence as any theory in science.

But what would Darwin have written had he been obliged to write a proposal to fund his voyage on HMS Beagle? He didn’t have the hypothesis of natural selection yet—it grew out of the very observations he was setting out to make. If he wrote, truthfully, that “the isolated islands we will visit are excellent natural laboratories to observe what becomes of species introduced to a new locale,” it would be judged by today’s standards as a fishing expedition without a strong hypothesis.

What did Newton hypothesize, despite his protests to the contrary? He identified the right variables for the problem of planetary motion: force and momentum. Newton’s grant proposal might have read: “I hypothesize that momenta and forces are the right variables to describe the motion of the planets. I propose to develop mathematical methods to predict their orbits, which I will compare with existing observations.” That’s not quite a guess about how nature works, but rather the best way to describe motion mathematically, which by its widespread success grew into intuitive concepts of force, momentum, and energy.

Newton wrote hypotheses non fingo because of what he didn’t hypothesize. He wrote in reaction to vortex theories of gravity originated by René Descartes and Christiaan Huygens. They imagined that so-called empty space was actually filled with swirling vortices of invisible particles that swept the planets along in their orbits. The vortex idea is certainly a guess about how gravity works; it’s just not a very helpful guess. The idea of invisible particles that only reveal themselves by effects on unreachably distant planets is too elastic a notion. It’s not specific enough to make testable predictions. In the language of 20th-century philosopher of science Karl Popper, it’s not readily falsifiable.

Newton didn’t provide a just-so story, a fanciful mechanism for why momentum was conserved or how gravity arose. Instead he formulated simple rules that describe how the planets move—and as it turns out, how nearly everything else moves under ordinary circumstances. Powerful as Newton’s insight was, his description of gravity had the unsettling feature of “spooky action at a distance” of the Sun on the planets, and indeed every mass on every other mass. It took another 250 years for an explanation of the physical origin of gravity.

Albert Einstein’s hypothesis about gravity, unlike Newton’s, was mechanistic: Mass curves space, which is slightly elastic; as a result, straight lines bend near massive objects, including the path of light from distant stars passing near the Sun on its way to our telescopes. It took years for Einstein to develop the math to show that Newton’s description, which was consistent with so many observations, was only an approximation—and to make astounding predictions of things that happen to huge masses (collapse into black holes) or when big masses move really fast (gravitational waves).

Setting physical science apart

So why is present-day funding so focused on hypothesis-driven research? A clue is that hypothesis-driven experimental design is best suited to certain influential fields, especially molecular biology and medicine. Researchers in those fields study complicated, irreducible systems (living organisms), have limited experimental probes, and are often forced to work with small data sets. Unavoidably, the most common experimental protocol in these fields is to poke at a complex living system by giving it a drug or chemical and then measuring some indirectly related response. Those experiments live and die by the statistical test. When a scatter plot of stimulus versus response looks like a cloud of angry bees, the formal discipline of testing the null hypothesis is essential.

Charles Darwin’s fateful voyage on HMS Beagle, illustrated here on a stop in Tierra del Fuego, might not have happened if Darwin had been forced to make a hypothesis-driven proposal for funding his place on the ship. Credit: Life and Letters of Charles Darwin (1888)

That is an overly narrow paradigm for what experiments can be. In the physical sciences, we are more able to manipulate and simplify the system of interest. We also enjoy more powerful experimental techniques, in many ways extensions of human senses, allowing us to see into a material, to listen to how it rings in response to being pinged with electromagnetic fields, to feel how it responds to a gentle push on the nanoscale. When you can do those things, experiments can be so much more than testing whether changing X influences Y with statistical significance. In fact, the history of science can be viewed as the development of new ways to probe nature. The Hubble Space Telescope was not driven by a hypothesis but rather by a desire to see deeper into the universe. Observations from Hubble and other modern telescopes enable new hypotheses about the early universe to be formulated and tested.

Progress in science often depends on advances in how to measure something important. A century after Einstein, ultrasensitive detectors brilliantly confirmed his prediction of gravitational waves. Those detectors rely on clever ideas for using lasers and interferometry to measure extremely tiny changes in the distance between two points on Earth. That work was not hypothesis driven, except in the obvious sense that general relativity predicts gravitational waves. Likewise, progress in quantitative sciences often relies on advances in our ability to compute the consequences of hypotheses that already exist.

Hypotheses are all well and good. But in evaluating research proposals, the key criterion should be: Will the proposed work help us answer an important question or reveal an important new question we should have been asking all along?

Scott Milner is William H. Joyce Chair and Professor of Chemical Engineering at the Pennsylvania State University.