Dave asked a bunch of very interesting questions in his recent post. These questions are probing about the nature of science and how science is done over the long-term. I think that a lot of people understand about science in the abstract – you ask a question (typically a yes/no question) and then think of some way of answering this question. This is a pretty picture of how people do science at a microscopic level, but it doesn’t address how people come up with the questions to ask. That, I think, is the tricky bit.
Let’s take the most obvious analogy that I can think of: a forest. Let’s pretend for a few minutes that no one has ever heard of a forest or trees. One day, someone wanders over a hill into a valley and notices these tall brown and green things in front of them. No one has ever seen these things before. The person takes a bunch of pictures, does some rough analysis of the heights of the trees and maybe how many there are (very rough!) and publishes a paper in Nature. A new field of science is born!
Scientists everywhere flock to the forest. There are a wide variety of papers that come out, covering topics such as: (a) bark – the skin of trees; (b) how tall is a tree, really; (c) rings – what are those all about; (d) leaves – it’s all about the shape; (e) can animals survive in the darkness of trees; (e) on the size distribution of conifers of the upper valley; (f) a detailed analysis of the bark from tree 12,362; (g) a detailed analysis of the leaf distribution from tree 12,362; and (h) the life cycle of tree: a statistical analysis. You get the idea – there are just a mountain of papers. No one has heard of trees, let alone forests! So, there is a ton of new things to investigate. Some of those papers do a detailed analysis of single trees and generalize to every other tree, while others do statistical analysis of all (or a subsample) of the trees. Every paper is new and fresh and exciting.
After 20 years of studying the forest, you have some scientists who are still looking at tree 12,362, and writing papers on how that tree has changed over the course of 20 years, and others who are looking at a statistical analysis of how much sunlight is needed to support the robust growth of poison ivy (the scourge of the forest!). Another study argues that the analysis of the study that was done 15 years ago was flawed and instead of 1,250,320 trees in the forest, there really are 1,261,624. There is a vicious rebuttal.
After 40 years, the papers start to focus on forest management and what we can do to sustainably harvest the wood for houses and fires and other things, but yet keep the biodiversity of the forest. There are occasional papers on new species of trees and animals that come out, but they are relatively few and far in between. It is becoming harder to get funding for fundamental tree research. The public in general is still pretty excited by trees and forests, but we know a lot about them, so we don’t need to spend as much money on fundamental research for this specific topic. Textbooks are written, and the topic is covered in classes throughout high school and college.
This is the natural order of science topics – an initial discovery is made, people flock to the field to study it, lots of basic science is done to explore the topic, with funding to support the new science, then, as more and more is known about the subject, funding starts to decrease, papers discuss more and more about the details of the subject, with fewer fundamental discoveries, the knowledge is accumulated in textbooks, and eventually people turn to different science topics. It is a lifecycle. Many science topics result in practical applications. For example, atomic physics. One of the practical applications is the ability to kill hundreds of thousands of people with a very small device. I supposed I could have come up with a better example.
In the 1940s, the first rockets that went into space made measurements of the upper atmosphere and the magnetosphere. These rockets couldn’t get very far away from the Earth, so they were basically constrained to studying these regions. There were a LOT of them. We made a ton of fundamental discoveries of the thermosphere, ionosphere, and magnetosphere. As we moved into the 1970s, we sent missions to Mars and to fly by other planets like Jupiter, Saturn, Neptune, and Uranus. We took pictures of the sun from above the atmosphere and discovered what the sun looks like in X-ray wavelengths. In the 1980s we took images of the northern (and southern!) lights from space. We measured the winds and temperatures in the upper atmosphere. We were discovering new species of trees everywhere we looked. With more satellite launches, radars deployed, lidars built, and other instruments spread across the globe.
Today, NASA’s budget is less than 1/10th the size it was in 1969. We have been to the moon, then decided it was not worth the expense. We have measured all sorts of interesting things in space. We’ve done a pretty good job of classifying the trees – improving our understanding of the near-Earth space environment. Does this mean that it is time to stop doing research on the space environment, since we understand a bunch of the large-scale physics of the system?
I think that this is an interesting discussion. At this time, we spend several billion dollars a year on measuring the weather down here where we live. In many ways, this is not to improve our understanding of the atmosphere (although this data definitely helps!), but it is in order to enable us to specify the weather status right now and predict what the weather will be like in a few days from now. This is obviously important for many, many people.
Specifying the weather in space is not super important to the vast majority of people right now. There are some areas where it is important, though. For example, trying to predict when and if satellites or pieces of orbital debris will collide. In order to figure this out, it is quite important to understand the weather in the upper atmosphere. If you would like airplanes and cars to reliably use GPS in an automated way, then understanding the state of the ionosphere becomes important.
In some ways this discussion of the importance of space research becomes an argument for the transition of the pure research to the specification and prediction of space. There will clearly need to be science that is done to improve our understanding of the system. For example, meteorologists can explain how a tornado forms, but to predict this is almost impossible. More research is needed in order to more fully explain the exact conditions, with bounds on those conditions, that lead to different sizes of tornados. Science improves our ability to predict. The motivation that drives the science can be both the desire to better understand the physical processes and the desire to improve the nation’s ability to predict what will happen in the future.
We are at a cross-roads in the space physics community, where one road is called Specification and Prediction, while the other is called Double Down on Basic Physics. I personally think that we should explore both paths and that it is ok to have science that is motivated by practical applications and not just the desire to know more.
Dave – you asked a lot more questions than just this really “simple” one that I answered. I think that you have started an interesting discussion that I hope you will pick up! I really look forward to hearing your thoughts on this and other topics that you raised.