## How hard is space travel, in principle?

Our Earth-based intuitions about the difficulty of travelling long distances break down badly in space. It’s tempting to think that just because Saturn, say, is nearly 4,000 times further away than the moon, it must be 4,000 times more difficult to reach. After all, on Earth it takes about 10 times as much work to go 10 kilometers as it does to go 1 kilometer. But in space, where there is no friction, this intuition is entirely wrong. In fact, in this essay I’ll show that with some important caveats the situation is far more favourable, and it doesn’t take all that much more energy to get to the outer planets than it does to get to low-Earth orbit.

The numbers are striking. We’ll see that it takes about 10 times as much energy to get to the moon as it does to get to low-Earth orbit. About 4 times more energy than that will get you to Mars, despite the fact that Mars is more than 200 times further away than the moon. Tripling that energy gets you all the way out to Saturn! So in some sense, the gap between getting to the moon and getting to Saturn isn’t really all that much different from the difference between getting into low-Earth orbit and getting to the moon.

The calculations required to obtain these results are all simple calculations in Newtonian gravitation, and they’re done in the next section. If you want to skip the details of the calculations, you should move to the final section, where I discuss some important caveats. In particular, we’ll see that just because getting to Saturn requires only 12 times as much energy as getting to the moon doesn’t mean that we only need to build rockets twelve times as big. The situation is more complex than that, and depends on the details of the propulsion technologies used.

### Calculations

To see why the numbers I quoted above are true, we need to figure out how much energy is required to get into low-Earth orbit. I will assume that the only obstacle to getting there is overcoming the Earth’s gravitation. In actual fact, of course, we need to overcome many other forces as well, most notably atmospheric friction, which adds considerably to the energy cost. I’ll ignore those extra forces – because the cost of getting to low-Earth orbit is the yardstick I’m using to compare with other possibilities this will mean that my analysis is actually quite pessimistic.

Suppose we have a mass $$m$$ that we want to send into space. Let’s use $$m_E$$ to denote the mass of the Earth. We suppose the radius of the Earth is $$r_E$$ and that we want to send our mass to a radius $$d r_E$$ for some $$d > 1$$. We’ll call $$d$$ the distance parameter – it’s the distance from the center of the Earth that we want to send our mass to, measured in units of the Earth’s radius. For instance, if we want to send the mass to a height of $$600$$ kilometers above the Earth’s surface, then $$d = 1.1$$, since the Earth’s radius is about $$6,000$$ kilometers. The energy cost to do this is $$Gm_Em/r_E-Gm_Em/ d r_E$$, where $$G$$ is Newton’s gravitational constant. We can rewrite this energy cost as:

$$e_d = \frac{Gm_em}{r_E} (1-1/d)$$

We can use this formula to analyse both the energy cost to send an object to low-Earth orbit and also to the moon. (We can do this because in going to the moon the main barrier to overcome is also the Earth’s gravitation). Suppose $$d_l$$ is the distance parameter for low-Earth orbit, let’s say $$d_l = 1.1$$, as above, and $$d_m$$ is the distance parameter for the moon, $$d_m = 60$$. Then the ratio of the energy cost to go to the moon as opposed to the energy cost for low-Earth orbit is:

$$\frac{e_{d_m}}{e_{d_l}} = \frac{1-1/d_m}{1-1/d_l} = 10$$.

That is, it takes $$10$$ times as much energy to get to the moon as to get to low-Earth orbit.

What about if we want to go further away, outside the influence of the Earth’s gravitational field, but still within the sun’s gravitational field? For instance, what if we want to go to Mars or Saturn? For those cases we’ll do a similar calculation, but in terms of parameters relevant to the gravitational field of the sun, rather than the Earth – to avoid confusion, I’ll switch to using upper case letters to denote those parameters, where before I used lower-case letters. In particular, let’s use $$M_s$$ to denote the mass of the sun, and $$R_e$$ to denote the radius at which the Earth orbits the sun. Let’s suppose we want to send a mass $$m$$ to a distance $$D R_e$$ from the sun, i.e., now we’re measuring distance in units of the radius of the Earth’s orbit around the sun, not the radius of the Earth itself. The energy cost to do this is [1]:

$$E_D = \frac{GM_sm}{R_e}(1-1/D)$$

The ratio of the energy required to go to a distance $$DR_E$$ from the sun versus the energy required to reach low-Earth orbit is thus:

$$\frac{E_{D}}{e_{d_l}} = \frac{M_sr_e}{m_e R_e}\frac{1-1/D}{1-1/d_l}$$

Now the sun is about $$330,000$$ times as massive as the Earth. And the radius of the Earth’s orbit around the sun is about $$25,000$$ times the radius of the Earth. Substituting those values we see that:

$$\frac{E_{D}}{e_{d_l}} = 13 \frac{1-1/D}{1-1/d_l}$$

For Mars, $$D$$ is roughly $$1.5$$, and this tells us that the energy cost to get to Mars is roughly $$40$$ times the energy cost to get to low-Earth orbit (but see footnote [1], below, if you haven’t already). For Saturn, $$D$$ is roughly $$10$$, and so the energy cost to get to Saturn is roughly $$120$$ times the energy cost to get to low-Earth orbit. For the stars, $$D$$ is infinity, or close enough to make no difference, and so the energy cost to get to the stars is only about 10 percent more than the cost to get to Saturn! Of course, with current propulsion technologies it might take rather a long time to get to the stars.

### Caveats

There are important caveats to the results above. Just because sending a payload to Mars only requires giving it about four times more energy than sending it to the moon, it doesn’t follow that if you want to send it on a rocket to Mars then you’ll only need about four times as much rocket fuel. In fact, nearly all of the energy expended by modern rockets goes into lifting the rocket fuel itself, and only a small amount into the payload. An unfortunate consequence of this is that you need a lot more than four times as much fuel – either that, or a much more efficient propulsion system than the rockets we have today. In a way, we’ve been both very lucky and very unlucky with our rockets. We’ve been lucky because our propulsion systems are just good enough to be able to carry tiny payloads into space, using enormous quantities of fuel. And we’ve been unlucky because to give those payloads even a tiny bit more of the energy they need to go further requires a lot more fuel. See, e.g., ref,ref and the pointers therein for more discussion of these points.

The extent to which any of this is a problem depends on your launch technology. Ideas like space guns and the space elevator don’t require any fuel to be carried along with the payload, and so escape the above problem. Of course, they’re also still pretty speculative ideas at this point! Still, I think it’s an interesting observation that the energy required to get a large mass to a distant part of the solar system is not, in principle, all that far beyond what we’ve already achieved in getting to the moon.

### Footnote

[1] Note that the object needs to first escape out of the Earth’s gravitational field, and this imposes an extra energy cost. This extra cost is roughly 10 times the cost of getting to low Earth orbit, by a calculation similar to that we did for getting to the moon. Strictly speaking, this energy cost should be added on to the numbers we’ll derive later for Mars and Saturn. But for the rough-and-ready calculation I’m doing, I won’t worry about it – we’re trying to get a sense for orders of magnitude here, not really detailed numbers!

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## The mismeasurement of science

Albert Einstein’s greatest scientific “blunder” (his word) came as a sequel to his greatest scientific achievement. That achievement was his theory of gravity, the general theory of relativity, which he introduced in 1915. Two years later, in 1917, Einstein ran into a problem while trying to apply general relativity to the Universe as a whole. At the time, Einstein believed that on large scales the Universe is static and unchanging. But he realized that general relativity predicts that such a Universe can’t exist: it would spontaneously collapse in on itself. To solve this problem, Einstein modified the equations of general relativity, adding an extra term involving what is called the “cosmological constant”, which, roughly speaking, is a type of pressure which keeps a static Universe from collapsing.

Twelve years later, in 1929, Edwin Hubble discovered that the Universe isn’t static and unchanging, but is actually expanding. Upon hearing the news, Einstein quickly realized that if he’d taken his original 1915 theory seriously, he could have used it to predict the expansion that Hubble had observed. That would have been one of the great theoretical predictions of all time! It was this realization that led Einstein to describe the cosmological constant as the “biggest blunder” of his life.

The story doesn’t end there. Nearly seven decades later, in 1998, two teams of astronomers independently made some very precise measurements of the expansion of the Universe, and discovered that there really is a need for the cosmological constant (ref,ref). Einstein’s “biggest blunder” was, in fact, one of his most prescient achievements.

The point of the story of the cosmological constant is not that Einstein was a fool. Rather, the point is that it’s very, very difficult for even the best scientists to accurately assess the value of scientific discoveries. Science is filled with examples of major discoveries that were initially underappreciated. Alexander Fleming abandoned his work on penicillin. Max Born won the Nobel Prize in physics for a footnote he added in proof to a paper – a footnote that explains how the quantum mechanical wavefunction is connected to probabilities. That’s perhaps the most important idea anyone had in twentieth century physics. Assessing science is hard.

### The problem of measuring science

Assessing science may be hard, but it’s also something we do constantly. Countries such as the United Kingdom and Australia have introduced costly and time-consuming research assessment exercises to judge the quality of scientific work done in those countries. In just the past few years, many new metrics purporting to measure the value of scientific research have been proposed, such as the h-index, the g-index, and many more. In June of 2010, the journal Nature ran a special issue on such metrics. Indeed, an entire field of scientometrics is being developed to measure science, and there are roughly 1,500 professional scientometricians.

There’s a slightly surreal quality to all this activity. If even Einstein demonstrably made enormous mistakes in judging his own research, why are the rest of us trying to measure the value of science systematically, and even organizing the scientific systems of entire countries around these attempts? Isn’t the lesson of the Einstein story that we shouldn’t believe anyone who claims to be able to reliably assess the value of science? Of course, the problem is that while it may be near-impossible to accurately evaluate scientific work, as a practical matter we are forced to make such evaluations. Every time a committee decides to award or decline a grant, or to hire or not hire a scientist, they are making a judgement about the relative worth of different scientific work. And so our society has evolved a mix of customs and institutions and technologies to answer the fundamental question: how should we allocate resources to science? The answer we give to that question is changing rapidly today, as metrics such as citation count and the h-index take on a more prominent role. In 2006, for example, the UK Government proposed changing their research assessment exercise so that it could be done in a largely automated fashion, using citation-based metrics. The proposal was eventually dropped, but nonetheless the UK proposal is a good example of the rise of metrics.

In this essay I argue that heavy reliance on a small number of metrics is bad for science. Of course, many people have previously criticised metrics such as citation count or the h-index. Such criticisms tend to fall into one of two categories. In the first category are criticisms of the properties of particular metrics, for example, that they undervalue pioneer work, or that they unfairly disadvantage particular fields. In the second category are criticisms of the entire notion of quantitatively measuring science. My argument differs from both these types of arguments. I accept that metrics in some form are inevitable – after all, as I said above, every granting or hiring committee is effectively using a metric every time they make a decision. My argument instead is essentially an argument against homogeneity in the evaluation of science: it’s not the use of metrics I’m objecting to, per se, rather it’s the idea that a relatively small number of metrics may become broadly influential. I shall argue that it’s much better if the system is very diverse, with all sorts of different ways being used to evaluate science. Crucially, my argument is independent of the details of what metrics are being broadly adopted: no matter how well-designed a particular metric may be, we shall see that it would be better to use a more heterogeneous system.

As a final word before we get to the details of the argument, I should perhaps mention my own prejudice about the evaluation of science, which is the probably not-very-controversial view that the best way to evaluate science is to ask a few knowledgeable, independent- and broad-minded people to take a really deep look at the primary research, and to report their opinion, preferably while keeping in mind the story of Einstein and the cosmological constant. Unfortunately, such a process is often not practically feasible.

### Three problems with centralized metrics

I’ll use the term centralized metric as a shorthand for any metric which is applied broadly within the scientific community. Examples today include the h-index, the total number of papers published, and total citation count. I use this terminology in part because such metrics are often imposed by powerful central agencies – recall the UK government’s proposal to use a citation-based scheme to assess UK research. Of course, it’s also possible for a metric to be used broadly across science, without being imposed by any central agency. This is happening increasingly with the h-index, and has happened in the past with metrics such as the number of papers published, and the number of citations. In such cases, even though the metric may not be imposed by any central agency, it is still a central point of failure, and so the term “centralized metric” is appropriate. In this section, I describe three ways centralized metrics can inhibit science.

Centralized metrics suppress cognitive diversity: Over the past decade the complexity theorist Scott Page and his collaborators have proved some remarkable results about the use of metrics to identify the “best” people to solve a problem (ref,ref). Here’s the scenario Page and company consider. Suppose you have a difficult creative problem you want solved – let’s say, finding a quantum theory of gravity. Let’s also suppose that there are 1,000 people worldwide who want to work on the problem, but you have funding to support only 50 people. How should you pick those 50? One way to do it is to design a metric to identify which people are best suited to solve the problem, and then to pick the 50 highest-scoring people according to that metric. What Page and company showed is that it’s sometimes actually better to choose 50 people at random. That sounds impossible, but it’s true for a simple reason: selecting only the highest scorers will suppress cognitive diversity that might be essential to solving the problem. Suppose, for example, that the pool of 1,000 people contains a few mathematicians who are experts in the mathematical field of stochastic processes, but who know little about the topics usually believed to be connected to quantum gravity. Perhaps, however, unbeknownst to us, expertise in stochastic processes is actually critical to solving the problem of quantum gravity. If you pick the 50 “best” people according to your metric it’s likely that you’ll miss that crucial expertise. But if you pick 50 people at random you’ve got a chance of picking up that crucial expertise [1]. Richard Feynman made a similar point in a talk he gave shortly after receiving the Nobel Prize in physics (ref):

If you give more money to theoretical physics it doesn’t do any good if it just increases the number of guys following the comet head. So it’s necessary to increase the amount of variety… and the only way to do it is to implore you few guys to take a risk with your lives that you will never be heard of again, and go off in the wild blue yonder and see if you can figure it out.

What makes Page and company’s result so striking is that they gave a convincing general argument showing that this phenomenon occurs for any metric at all. They dubbed the result the diversity-trumps-ability theorem. Of course, exactly when the conclusion of the theorem applies depends on many factors, including the nature of the cognitive diversity in the larger group, the details of the problem, and the details of the metric. In particular, it depends strongly on something we can’t know in advance: how much or what type of cognitive diversity is needed to solve the problem at hand. The key point, though, is that it’s dangerously naive to believe that doing good science is just a matter of picking the right metric, and then selecting the top people according to that metric. No matter what the metric, it’ll suppress cognitive diversity. And that may mean suppressing knowledge crucial to solving the problem at hand.

Centralized metrics create perverse incentives: Imagine, for the sake of argument, that the US National Science Foundation (NSF) wanted to encourage scientists to use YouTube videos as a way of sharing scientific results. The videos could, for example, be used as a way of explaining crucial-but-hard-to-verbally-describe details of experiments. To encourage the use of videos, the NSF announces that from now on they’d like grant applications to include viewing statistics for YouTube videos as a metric for the impact of prior research. Now, this proposal obviously has many problems, but for the sake of argument please just imagine it was being done. Suppose also that after this policy was implemented a new video service came online that was far better than YouTube. If the new service was good enough then people in the general consumer market would quickly switch to the new service. But even if the new service was far better than YouTube, most scientists – at least those with any interest in NSF funding – wouldn’t switch until the NSF changed its policy. Meanwhile, the NSF would have little reason to change their policy, until lots of scientists were using the new service. In short, this centralized metric would incentivize scientists to use inferior systems, and so inhibit them from using the best tools.

The YouTube example is perhaps fanciful, at least today, but similar problems do already occur. At many institutions scientists are rewarded for publishing in “top-tier” journals, according to some central list, and penalized for publishing in “lower-tier” journals. For example, faculty at Qatar University are given a reward of 3,000 Qatari Rials (US \$820) for each impact factor point of a journal they publish in. If broadly applied, this sort of incentive would creates all sorts of problems. For instance, new journals in exciting emerging fields are likely to be establishing themselves, and so have a lower impact factor. So the effect of this scheme will be to disincentivize scientists from participating in new fields; the newer the field, the greater the disincentive! Any time we create a centralized metric, we yoke the way science is done to that metric.

Centralized metrics misallocate resources: One of the causes of the financial crash of 2008 was a serious mistake made by rating agencies such as Moody’s, S&P, and Fitch. The mistake was to systematically underestimate the risk of investing in financial instruments derived from housing mortgages. Because so many investors relied on the rating agencies to make investment decisions, the erroneous ratings caused an enormous misallocation of capital, which propped up a bubble in the housing market. It was only after homeowners began to default on their mortgages in unusually large numbers that the market realized that the ratings agencies were mistaken, and the bubble collapsed. It’s easy to blame the rating agencies for this collapse, but this kind of misallocation of resources is inevitable in any system which relies on centralized decision-making. The reason is that any mistakes made at the central point, no matter how small, then spread and affect the entire system.

In science, centralization also leads to a misallocation of resources. We’ve already seen two examples of how this can occur: the suppression of cognitive diversity, and the creation of perverse incentives. The problem is exacerbated by the fact that science has few mechanisms to correct the misallocation of resources. Consider, for example, the long-term fate of many fashionable fields. Such fields typically become fashionable as the result of some breakthrough result that opens up many new research possiblities. Encouraged by that breakthrough, grant agencies begin to invest heavily in the field, creating a new class of scientists (and grant agents) whose professional success is tied not just to the past success of the field, but also to the future success of the field. Money gets poured in, more and more people pursue the area, students are trained, and go on to positions of their own. In short, the field expands rapidly. Initially this expansion may be justified, but even after the field stagnates, there are few structural mechanisms to slow continued expansion. Effectively, there is a bubble in such fields, while less fashionable ideas remain underfunded as a result. Furthermore, we should expect such scientific bubbles to be more common than bubbles in the financial market, because decision making is more centralized in science. We should also expect scientific bubbles to last longer, since, unlike financial bubbles, there are few forces able to pop a bubble in science; there’s no analogue to the homeowner defaults to correct the misallocation of resources. Indeed, funding agencies can prop up stagnant fields of research for decades, in large part because the people paying the cost of the bubble – usually, the taxpayers – are too isolated from the consequences to realize that their money is being wasted.

### One metric to rule them all

No-one sensible would staff a company by simply applying an IQ test and employing whoever scored highest (c.f., though, ref). And yet there are some in the scientific community who seem to want to move toward staffing scientific institutions by whoever scores highest according to the metrical flavour-of-the-month. If there is one point to take away from this essay it is this: beware of anyone advocating or working toward the one “correct” metric for science. It’s certainly a good thing to work toward a better understanding of how to evaluate science, but it’s easy for enthusiasts of scientometrics to believe that they’ve found (or will soon find) the answer, the one metric to rule them all, and that that metric should henceforth be broadly used to assess scientific work. I believe we should strongly resist this approach, and aim instead to both improve our understanding of how to assess science, and also to ensure considerable heterogeneity in how decisions are made.

One tentative idea I have which might help address this problem is to democratize the creation of new metrics. This can happen if open science becomes the norm, so scientific results are openly accessible, online, making it possible, at least in principle, for anyone to develop new metrics. That sort of development will lead to a healthy proliferation of different ideas about what constitutes “good science”. Of course, if this happens then I expect it will lead to a certain amount of “metric fatigue” as people develop many different ways of measuring science, and there will be calls to just settle down on one standard metric. I hope those calls aren’t heeded. If science is to be anything more than lots of people following the comet head, we need to encourage people to move in different directions, and that means valuing many different ways of doing science.

Update: After posting this I Googled my title, out of curiosity to see if it had been used before. I found an interesting article by Peter Lawrence, which is likely of interest to anyone who enjoyed this essay.

### Acknowledgements

Thanks to Jen Dodd and Hassan Masum for many useful comments. This is a draft of an essay to appear in a forthcoming volume on reputation systems, edited by Hassan Masum and Mark Tovey.

### Footnotes

[1] Sometimes an even better strategy will be a mixed strategy, e.g., picking the top 40 people according to the metric, and also picking 10 at random. So far as I know this kind of mixed strategy hasn’t been studied. It’s difficult to imagine that the proposal to pick, say, one in five faculty members completely at random is going to receive much support at Universities, no matter how well founded the proposal may be. We have too much intuitive sympathy for the notion that the best way to generate global optima is to locally optimize. Incidentally, the success of such mixed strategies is closely related to the phenomenon of stochastic resonance, wherein adding a noise to a system can sometimes improve its performance.

My book “Reinventing Discovery” will be released in 2011. It’s about the way open online collaboration is revolutionizing science. A summary of many of the themes in the book is available in this essay. If you’d like to be notified when the book is available, please send a blank email to the.future.of.science@gmail.com with the subject “subscribe book”. You can subscribe to my blog here, and to my Twitter account here.