Elsevier

Medical Hypotheses

Volume 75, Issue 6, December 2010, Pages 482-489
Medical Hypotheses

The unreasonable effectiveness of my self-experimentation

https://doi.org/10.1016/j.mehy.2010.04.030Get rights and content

Summary

Over 12 years, my self-experimentation found new and useful ways to improve sleep, mood, health, and weight. Why did it work so well? First, my position was unusual. I had the subject-matter knowledge of an insider, the freedom of an outsider, and the motivation of a person with the problem. I did not need to publish regularly. I did not want to display status via my research. Second, I used a powerful tool. Self-experimentation about the brain can test ideas much more easily (by a factor of about 500,000) than conventional research about other parts of the body. When you gather data, you sample from a power-law-like distribution of progress. Most data helps a little; a tiny fraction of data helps a lot. My subject-matter knowledge and methodological skills (e.g., in data analysis) improved the distribution from which I sampled (i.e., increased the average amount of progress per sample). Self-experimentation allowed me to sample from it much more often than conventional research. Another reason my self-experimentation was unusually effective is that, unlike professional science, it resembled the exploration of our ancestors, including foragers, hobbyists, and artisans.

Introduction

In 1960, a physicist named Eugene Wigner published an essay called “The Unreasonable Effectiveness of Mathematics in the Natural Sciences” [1]. Mathematics invented to describe one thing, said Wigner, had often turned out to provide a good description of something much different. He could not explain this. I have been puzzled in a similar way. Over 12 years (1990–2002), my self-experimentation found new ways to improve sleep, mood, health, and weight [2]. Four of the new ways (avoiding breakfast to reduce early awakening, seeing morning faces to improve mood, standing to reduce early awakening, and drinking sugar water to lose weight) were surprising; almost all were practical. In health, as in other areas of science, we expect progress to come from subject-matter experts (e.g., sleep researchers) with grants. Yet I was not an expert in what I studied and my research cost almost nothing. I did it in my spare time. In spite of this, my self-experimental research was far better than my mainstream research (e.g., [3], [4]). For a long time, this puzzled me. Now I propose an explanation.

The puzzle began in graduate school, where I studied experimental psychology. To learn how to do experiments, I tried to do as many as possible. At the time I had acne. It was easy to measure (count pimples each morning) so I decided to do experiments about it. My dermatologist had prescribed tetracycline, an antibiotic. A few months of self-experimentation showed that tetracycline did not work [5], which surprised my dermatologist. Later conventional research found that tetracycline often fails [6], [7]. My dermatologist had years of experience. Yet a little self-experimentation by a non-expert found something important that he and other dermatologists did not know.

I continued to self-experiment. I made little progress the first 10 years but plenty of progress the next 12 [2]. The new ideas suggested by my results included (from more to less important): 1. A theory about mood and depression. 2. A theory about weight control. 3. Seeing faces in the morning makes mood worse that evening and better the next day. 4. Sugar water causes weight loss. 5. Better sleep can greatly reduce colds. 6. Breakfast can cause early awakening. 7. Standing a lot reduces early awakening. 8. Ways to change the size of the faces effect. 9. Other weight-loss methods. Most of my conclusions were also supported by conventional research. Some of the weight-loss methods (such as drinking lots of water or eating lots of sushi) could not be sustained, but the rest were useful.

No well-known idea fully explains how much progress I made. Better equipment (e.g., microscope, interferometer) often produces new scientific ideas. I had used a personal computer (new at the time), which made data collection much easier. However, this was not sufficient to explain my unusual progress because most other scientists had also started to use personal computers. Kuhn [8] argued that the accumulation of inexplicable results helps generate progress. There is some truth to this. My weight-control theory was partly inspired by the hard-to-explain results of Ramirez [9]. I thought of my theory soon after learning about them. It was not that simple, however; I also did four experiments that supported the new theory. Moreover, my mood theory did not fit Kuhn’s pattern. It had nothing to do with inexplicable results. It was an obvious conclusion from the effects I had found. Sulloway [10] showed that later-borns are more likely than first-borns to do and support radical science. I am a first-born.

Nor was self-experimentation a sufficient explanation. Self-experimentation is not new [11], [12]. Almost all examples have involved dangerous drugs or medical procedures. For example, one man took arsenic to test an antidote [12]. Another man had a tooth extracted to test a new anesthetic [12]. My self-experimentation was safe. I studied treatments available to anyone. Previous self-experimentation had almost always confirmed the experimenter’s beliefs. Mine often surprised me. No doubt self-experimentation was necessary for my progress. But its age and availability (many scientists could have done what I did) implies it was not sufficient.

My explanation of effectiveness has three parts. First (circumstances): I was in a rare and powerful position. I had the subject-matter knowledge of an insider, the freedom of an outsider, and the motivation of someone with the problem. Second (method): Self-experimentation is powerful and self-experimentation about the brain even more powerful. Third (context): Some broader ideas will make clearer why this combination of position and method worked so well.

I was in an unusually good position to make progress. I had the subject-matter knowledge of an insider, the freedom of an outsider, and the motivation of someone with the problem.

I was not a sleep, mood, or weight expert but I was not naive. I was a professor of psychology at a research university. From teaching introductory psychology, I had learned about sleep, mood, and weight research. I also knew about sleep research because sleep is controlled by an internal clock and my research was about a (different) internal clock [3]. My conventional research had given me a good understanding of experimental design, measurement, and data analysis.

Four examples of how my knowledge helped: 1. In 1990, unusual data analysis showed that my sleep duration had decreased a few months earlier. This finding triggered a series of events that led to the discovery that breakfast caused early awakening. 2. Because I had done research with rats, I knew about a laboratory effect called anticipatory activity [13]. My breakfast discovery resembled anticipatory activity in humans. This made my conclusion (breakfast causes early awakening) far more plausible. 3. From teaching introductory psychology, I knew that depression and insomnia are closely linked. The linkage made it much more plausible that something I had done to improve sleep (watch TV in the morning) improved mood. 4. My knowledge of associative learning (the main topic of animal learning, my area of expertise within psychology) made it much easier to go from Ramirez’s results [9] to a new theory of weight control.

My self-experimentation was not my job. For a long time, I did not expect to publish it; even later, after I decided to, I did not plan to use it to gain status within a profession. This freed me to (a) do whatever worked and (b) take as long as necessary. Professional scientists cannot try anything and cannot take as long as necessary. As Dyson [14] said, “In almost all the varied walks of life, amateurs have more freedom to experiment and innovate [than professionals].”

Professional scientists are constrained in many ways. Most of their research with human and animal subjects needs to be approved by an internal review board, which may take 6 months. Every change in protocol must be approved. Most professional scientists need grants. As Lederberg [15, p. 337] said, “Only the most accomplished and fortunate [scientist] can look beyond the renewal of their research grant.” Most professional scientists need a steady stream of publications. To get tenure, you must publish a certain amount. To get your grant renewed, you must publish a certain amount. If you have graduate students, each should do publishable research. Two years to produce a paper might be okay but 10 years would be too long. It took me 10 years to begin to understand why I woke up too early. I tried one possible solution after another and eventually made progress. A professional sleep researcher could not have done this.

Professional scientists are also constrained by taboos. Alister Hardy was a biology professor at Oxford in the middle of the 1900s. Early in his career, he came up with the aquatic ape theory of human evolution. He said nothing about it, however. “I wanted to be a professor. I wanted to be a Fellow of the Royal Society,” he explained [16, p. 13]. After 30 years, he had achieved these goals, so he felt free to give a talk about his theory. A journalist happened to attend and wrote about it. One of his colleagues was upset and phoned Hardy. Never do that again! he told him. Hardy’s crazy theory had made Oxford look bad. At Hardy’s memorial service, his theory was not mentioned [16, p. 14]. Because I was not a sleep, mood, or weight researcher, I did not care what they found unacceptable. Perhaps they consider self-experimentation unacceptable.

Major scientific advances are often linked to unusual freedom. Mendel’s job as a monk gave him botanical freedom. His colleagues did not care about his pea plants nor what he wrote about them. Likewise, Charles Darwin could write whatever he wanted, unlike biology professors. His wealth and lack of job meant he had little to lose. Alfred Wegener, who proposed continental drift, was a meteorologist, not a geologist. His geological heresy surely did not bother his colleagues. Mendel, Darwin, and Wegener illustrate Dyson’s point about the freedom of hobbyists.

I did self-experimentation to improve my own life (e.g., sleep better). In contrast, professional scientists almost never study their own problems. They have other goals.

On the face of it, professional scientists should embrace self-experimentation. It would make their life easier. No need for grants or graduate students. Not only is self-experimentation easier, it allows study of a wider range of questions. If you have tenure, you can afford to do slow, risky research. Why is long-term self-experimentation like mine not more popular?

In The Theory of the Leisure Class [17], Veblen argued that upper-class persons, such as professors, take considerable pains to show their social position. They do so in three ways: 1. Display wealth. Veblen coined the term conspicuous consumption. Tail fins do not improve a car’s nominal function (transportation) but do show wealth. 2. Display uselessness. The customs of long fingernails (women) and ties (men), said Veblen, arose because both show that their possessors do not do manual labor (useful), with which long nails and ties would interfere. 3. Display refinement. You display refinement via activities that are conspicuous, time-consuming, and of little value. Display of useless knowledge such as “knowledge of the dead languages and the occult sciences; of correct spelling; of syntax and prosody; of the various forms of domestic music and other household art; of the latest properties of dress, furniture, and equipage; of games, sports, and fancy-bred animals, such as dogs and race-horses” [17] were some of Veblen’s examples.

The last chapter of The Theory of the Leisure Class is about professors. As the term ivory tower indicates, most academic research lacks practical value (Rule 2). Several facts suggest that science professors follow Veblen’s rules. Not being wealthy, they cannot display wealth (Rule 1) but they can follow Rules 2 (uselessness) and 3 (refinement). Scientists distinguish between basic research (with no obvious value) and applied research (with obvious value); consistent with Veblen, basic research has higher status. To give a specific example, much of modern economics, especially the highly mathematical parts, has little obvious value [18]. “It’s academic,” a prominent economist said recently. “It is nothing like as useful to the business community as it could be” [18, p. 51]. Here academic means useless, as it does in the phrase of academic value. Although the Nobel Prize is supposed to be given for useful research, it is often given for research without clear practical value – the 2009 Medicine prize for telomere research, for example. After William Vickrey received the 1996 Nobel Prize in Economics, he told a journalist his prize-winning work was “at best … of minor significance in terms of human welfare” [18, p. 50]. According to John Cassidy, the New Yorker writer, the economics Nobel Prize “has fostered a professional culture that favors technical wizardry above all else” [18, p. 60] – above practical value, in particular. Veblen would say this tendency did not need much fostering. At the same time, research of great practical value, such as the discovery that smoking causes lung cancer, has not been given a Nobel Prize.

Technical wizardry without obvious value is an example of refinement. The wizardry took time to learn. In the field of statistics, professors emphasize complex numerical algorithms. Although such algorithms are much less useful than graphs [19], statistics texts are roughly 1% graphs, 99% complex numerical algorithms, reflecting how statistics professors spend their time. Likewise, scientists use unnecessary fancy words. When a scientist describes something as rufous rather than brown, he is showing refinement. Most people do not know what rufous means.

Veblen’s ideas help explain why self-experimentation is rare among professional scientists. It violates all three of his rules. Scientists cannot display great wealth (Rule 1), but they can at least hope to get a large grant, buy expensive equipment, and have many people working for them. Because of its low cost, self-experimentation does not facilitate that. Self-experimentation such as mine is obviously useful, violating Rule 2 (uselessness). And anyone can do it, violating Rule 3 (refinement). It is common, in the derogatory sense.

Veblenian tendencies push scientists away from self-experimentation and away from useful work. But if you have a health problem, you will surely care more about alleviating it than displaying status. Some examples suggest what a difference the change in motivation makes. Paolo Zamboni’s discovery of reduced blood flow in persons with multiple sclerosis [20] happened because his wife had multiple sclerosis. He was not a multiple-sclerosis expert. Dennis Mangan, a lab technician, found that mega-doses of niacin quickly cured his mother’s Restless Leg Syndrome [21], something not previously reported in the scientific literature. The most important example is home blood glucose testing, an enormous advance in the management of diabetes. It was pioneered by Richard Bernstein, at the time an engineer, who had diabetes himself [22].

My self-experimentation was more powerful than conventional research for four reasons. Two came from use of self-experimentation; the other two from studying measures (sleep, mood, and weight) controlled by the brain. (Variation in weight is mainly variation in body fat, which is controlled by hunger.)

First, self-experimentation is much easier than conventional research. It allows you to test solutions to health problems much faster, more cheaply, and more flexibly. For example, self-experimentation can test a new way to lose weight much faster than conventional experimentation. In [2] I reported five self-experiments about weight control. I have also done a conventional weight-control experiment with six subjects. With the time and effort it took to do that experiment, perhaps I could have done 50 self-experiments.

Second, self-experimentation measures many things at once. We continuously monitor ourselves in many ways, in the sense that our brain receives input from thousands of nerves. Our bodies can malfunction in thousands of ways. We effortlessly notice many of them. Without trying, we notice our mood, clarity of thought, sleepiness, sleep quality, coordination, hunger, thirst, most of our skin, our digestion, how our joints feel, and so on. A conventional experiment measures far less. This wide-net feature of self-experimentation was responsible for my faces/mood discovery. One morning I watched TV because I thought it might improve my sleep; the next morning, without any special preparation, I noticed my mood was much better than usual. To quantify this, let us say we monitor ourselves in 100 separate ways. A conventional experiment measures perhaps five independent dimensions. In this way self-experimentation is 20 times more powerful than conventional experimentation.

Studying the brain rather than another part of the body gave me more advantages. The brain resembles a model system in two ways.

First, it changes quickly. The brain responds to external changes much faster than the rest of the body. Reaction-time experiments may put different treatments 10 s apart. In many of my rat experiments, which measured behavior, different trials involved different treatments; the trials were about a minute apart. A treatment may substantially improve brain function in hours. To substantially improve bone density might take months. Let us say the brain changes 10 times faster than other organs.

Second, it is easy to measure. The brain can be measured by measuring behavior, which I can do with my laptop. I cannot measure immune function, liver function, kidney function, bone density, heart attack risk, or dozens of other important health measures with my laptop. Perhaps the brain is 50 times easier to measure than other organs. (An exception is the skin, which is easy to measure. It makes sense that one of my examples of self-experimental power involved acne.)

The first two features make self-experimentation 1000 (50 × 20) more powerful than conventional research. The last two features make self-experimentation about the brain 500 (10 × 50) times more powerful than self-experimentation about other organs. The total improvement – self-experimentation about the brain compared to conventional research not about the brain – is 500,000 (1000 × 500). This means I could test 500,000 cause–effect relationships about the brain for the price that conventional researchers pay to test one cause–effect relationship about another part of the body. The combination of two big advantages (self-experimentation, brain) resembles the combination of fruit flies and salivary-gland chromosomes (much larger than other chromosomes) so helpful in the early study of genetics.

Parts 1 and 2 of this explanation do not explain two features of [2]. One is the large number of accidents (completely unexpected results). There were six: 1. When I changed my breakfast from oatmeal to fruit, my early awakening got worse. 2. When I stopped eating any breakfast, my early awakening almost disappeared. 3. When I watched TV early one morning, my mood improved the next day. 4. When I stood more, my sleep improved. 5. I mysteriously lost my appetite in Paris. 6. My theory of weight control, which helped me discover new ways to lose weight, was heavily based on Ramirez’s accidental discovery [9]. Why so many? The other unexplained feature is the way the rate of progress increased. It took 10 years to make one practical discovery (about breakfast and sleep); in the next 12 years I made about 10 more.

To explain these features, it helps to make assumptions behind Parts 1 and 2 more explicit. A context within which Parts 1 and 2 make sense has four assumptions.

Progress in science, as far as I can tell, is a mix of many tiny steps and a few big steps. When I have looked closely at big advances in understanding that led to practical discoveries, they were always built on a great deal of data. Each bit of data helped but there was great variation in how much. Almost all the observations were routine. They were unsurprising; they confirmed an idea already quite plausible. They repeated a well-known effect, for example. A small number were not routine; in some way they contradicted what was expected. Of that small number, most showed that a plausible idea was wrong. The Michaelson–Morley experiment, which disproved the ether theory, is an example. A small fraction of the small number immediately suggested a new idea. For example, the Geiger–Marsden experiment found that a few subatomic particles aimed at gold foil bounced backwards. It suggested a new theory of the structure of matter.

My own research resembled the historical examples. My discovery that breakfast caused early awakening (Example 1 in [2]) came from 10 years of trial and error. During those 10 years, I recorded my sleep most days. The sleep data I collected can be divided into three groups: (a) Tiny progress. I woke up too early thousands of times. In almost all cases, this was unsurprising but nevertheless contributed a tiny bit of progress, like a control group. (b) Medium-sized progress. Sometimes I tried a new solution to the problem – more exercise, for example. All my attempted solutions failed. That data contributed more than a tiny bit of progress; they showed that plausible beliefs were wrong. (c) Large progress. Two data sets were big steps forward: 1. When I started eating fruit for breakfast, early awakening increased. 2. When I stopped eating breakfast, early awakening nearly vanished.

These observations suggest that the distribution of scientific progress resembles a power-law (Pareto) distribution, which is linear on log–log coordinates (Fig. 1). You sample from the distribution when you gather data (everyday life, surveys, experiments). Most increases in knowledge are tiny, a tiny fraction are large. The largest ones are often called accidental, but Fig. 1 implies this is misleading. The simplicity of the function implies that all progress large (accidental), medium, or small comes from the same underlying process.

Specific evidence for such a distribution is, in addition to [2], the many medical examples described by Meyer [23]. Each of Meyer’s examples of medical progress involved many small steps and one large step. More evidence is the large number of non-medical examples where scientific progress came from an accident. The Wikipedia entry for serendipity lists 44 examples from biology, chemistry, physics, and astronomy. (Plus 15 from pharmacology, three from medicine not involving drugs, and nine from engineering.) For example, the first battery was made soon after Galvani noticed that a spark from a metal scalpel caused a dead frog’s leg to twitch – an accidental discovery. (And another example of the advantages of studying neurons.) Studying this phenomenon, he found that a frog’s muscles would twitch when it was in contact with two different metals. The first battery contained layers of different metals. A different sort of support for Fig. 1 is that the number of times a scientific paper is cited has a power-law distribution [24].

“Genius is one percent inspiration and ninety-nine percent perspiration,” said Thomas Edison. Fig. 1 says you need perspiration (a lot of sampling) to find inspiration (a big step forward). Tukey [25] distinguished exploratory data analysis (e.g., graphs) and confirmatory data analysis (e.g., t tests). Again, Fig. 1 says such distinctions are misleading. It says you generate ideas the same way you test them. For years, like Tukey, I believed that idea testing and idea generation required different methods. The title of [2] (“Self-experimentation as a source of new ideas”) reflects this distinction. It says self-experimentation is a good way to generate ideas – as if it were not a good way to test them. Table 1 of [2] says the same thing. Fig. 1 says I was wrong. The facts support Fig. 1. I used self-experimentation to test ideas many times. Most of the idea-generating accidents came when I was testing an idea. Ramirez’s surprising observations [9] happened while testing an idea.

The second assumption is that the slope of the progress distribution varies. It depends on what you know and do. Subject-matter knowledge flattens the distribution (left panel of Fig. 2). A sleep expert will learn more from one sleep datum than a non-expert. Pasteur’s “chance favors the prepared mind” is a subset of the left panel of Fig. 2, which says all data favor the prepared mind. In addition, scientific methods flatten the distribution. An experiment will produce more progress than the same amount of non-experimental data (right panel of Fig. 2). Likewise, better data analysis flattens the distribution. Such shifts of power-law-like distributions have been observed [4].

The idea that knowledge improves the slope explains why my rate of progress increased after 10 years. After 10 years of trial and error, I discovered that breakfast caused early awakening. This was a big step forward. I believe it improved the slope of my progress distribution because it increased my knowledge. It suggested that other powerful and beneficial treatments might be found among the elements of Stone-Age life. This idea led to three more discoveries (morning faces and mood, standing and sleep, sleep and colds).

The third assumption is that the rate of sampling from the distribution varies. Some methods allow more sampling than others. For example, a fast experimental design (e.g., a simple design) allows a higher sampling rate than a slow design (e.g., a more careful one). This might seem obvious, but in what I have read about experimental design sampling rate was never mentioned.

Assumptions 1–3 explain much of why my self-experimentation was unusually effective. The experts – sleep experts, for example – know more about the subject, use better equipment, and have more subjects per experiment than I do, so their distribution is flatter than mine. But their slope advantage is overwhelmed by my advantage in sampling rate.

Earlier I gave six examples (Mendel, Darwin, Wegener, Zamboni, Mangan, Bernstein) that suggested the importance of freedom and motivation. They were inside/outside correlations: Outsiders with unusual motivation or freedom made more progress than insiders. Within-profession correlations also exist, where insiders with unusual freedom or motivation make more progress than other insiders. In The New Yorker in 2006–7, Atul Gawande wrote two articles about medical innovation [26], [27]. The first [26] was about Apgar scores, which describe the health of a newborn baby. Since their introduction in 1953, Apgar scores have gradually improved, saving thousands of lives, even though, according to Gawande, obstetricians do not do research in the approved “evidence-based medicine” way. In addition, obstetricians are lower-status: “Doctors in other fields have always looked down their masked noses on their obstetrical colleagues,” wrote Gawande. Both features – less “correct” research methods and lower-status – suggest more freedom than usual (more freedom of research method) and unusual motivation (less desire for status because obstetricians chose a lower-status job within medicine). Gawande’s second article [27] was about the use of checklists to reduce surgical errors, which was pioneered by a doctor named Peter Pronovost. Asked why he did this work, Pronovost said his father had died from a medical error [28], an unusual motivation. Gawande did not mention this but did note the strangeness of Provonost’s work: no “multimillion-dollar grant”, no “swarm of doctoral students and lab animals” [26] – that is, no conspicuous wealth. “He’s focussed on work that is not normally considered a significant contribution in academic medicine,” wrote Gawande. “Yet his work has already saved more lives than that of any laboratory scientist in the past decade” [26]. Free from Veblenian tendencies, Provonost achieved highly-useful results.

Section snippets

A test of this explanation

In the previous sections, I have described the explanation and simple evidence for it. The rest of this article describes more complicated support (this section), related work (next section), and a broader but compatible explanation (“Science and Human Nature”).

A philosophical idea called Reichenbach’s Common Cause Principle helps explain rare events. It says if two events are correlated, either one causes the other or they have a common cause. Have a common cause means if you look at the

Related work

The idea that outsiders have more freedom than insiders has appeared in several forms. Veblen argued that the freedom enjoyed by outsiders gives them a problem-solving advantage [31]. Sulloway argued that later-borns are more likely to support radical science than first-borns because they are less invested in the status quo [10]. An experiment in an American lab found that students did better on a problem-solving task when told the problem came from Greece than when told it came from nearby [32]

Science and human nature

My explanation of the effectiveness of my self-experimentation can be summed up by saying I was in an unusual position and picked up an unusual tool. One rare event (unusual position plus unusual tool) caused another (unusual results). My work looks unusual, yes. If you read 1000 scientific articles, including mine, mine would stand out. But from another point of view, the other 999 articles are the outliers. Like most human activity, my self-experimentation fit well with human nature.

Conflict of interest statement

None.

Acknowledgement

I thank Glen Weyl for help.

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