I am writing a paper with a psychology professor friend of mine on why we should get amateurs (like myself) more involved in the “knowledge work” of psychological research (gathering observational data, designing and implementing experiments, generating hypotheses, data analysis, etc.) and how we can do so. There are a few pieces to the puzzle, but the simple answer of why we should get amateurs involved in psychology research is that, by virtue of being outsiders to academia, amateurs, are subject to very different constraints and incentives than the vast majority of professional researchers (professors, graduate students) and thus can think and work in ways that they might not be able to. It is precisely in these areas, which we refer to as “blind spots” (as in academia is systematically biased away from seeing/exploring these areas), where amateurs should work in order to advance psychology. Here, I will share a few sections from the draft where we propose different blind spots in academic psychology along with some additional commentary, but before I do that I want to flesh out this concept of a blind spot a little more and provide some examples.
Toward a Theory of Blind Spots
Imagine a landscape of all possible ideas…
(Did you actually try to imagine the landscape or did you just read the words?)
In this landscape, we may think of peaks as areas of good ideas (rational, useful, interesting, etc.) and valleys as bad ideas. Our challenge then, individually and collectively, is to optimize our exploration of the landscape. One thing that “landscape thinking” makes clear is the problem of being trapped on a local optima; the best strategy is not 100% hill-climbing—sometimes you need to go through a valley of bad ideas to find a new peak.
Blind spots are the regions in this landscape which are systematically unexplored or under-explored because of some constraint (either biological, psychological, social, political, economic) or incentive. Crucially, we can also think of blind spots as referring not just to areas of thought, but also to general ways of thinking, as untaken roads in the landscape of ideas. Identifying blind spots is useful because these are areas which may prove especially fruitful if given further thought—i.e. there may still be low-hanging fruit waiting to be picked.
I’ve begun to toy around with the idea of “blind spot thinking” as a kind of heuristic or mental model for directing one’s thinking to promising areas.
On an individual level, blind spot thinking requires you to ask yourself about what you don’t know or don’t appreciate because of who you are—what are the things I am systematically missing because of my identity and life history? Blind spot thinking can also be useful when thinking about your competitive advantage in a particular field or domain—what are the forces that bias people in this field away from thinking about certain things or thinking in certain kinds of ways? What blind spots are created by these biases? Do I have any skills/talents/interests that will allow me to explore these blind spots better than others?
The collective level—a country, an entire culture, or all of humanity—is where it really gets juicy: can we identify areas in the ideascape of ideas that massive groups of people (or all people ever) have overlooked? This is not an easy question to answer well—doing so amounts to finding a $100 bill hidden in plain sight, and that doesn’t happen often no matter how smart or knowledgeable you are. But if you can do it, the rewards are great (much greater than $100). In the best case scenario, the reward is a revolutionary idea, one that no person sees coming, the kind of idea that changes the world.
Though he doesn’t refer to it as blind spot thinking, Paul Graham’s essay “What Can’t You Say” is essentially a meditation on why we should actively seek out blind spots and how to do it.
Great work tends to grow out of ideas that others have overlooked, and no idea is so overlooked as one that's unthinkable. Natural selection, for example. It's so simple. Why didn't anyone think of it before? Well, that is all too obvious. Darwin himself was careful to tiptoe around the implications of his theory. He wanted to spend his time thinking about biology, not arguing with people who accused him of being an atheist.
In the sciences, especially, it's a great advantage to be able to question assumptions. The m.o. of scientists, or at least of the good ones, is precisely that: look for places where conventional wisdom is broken, and then try to pry apart the cracks and see what's underneath. That's where new theories come from.
A good scientist, in other words, does not merely ignore conventional wisdom, but makes a special effort to break it. Scientists go looking for trouble. This should be the m.o. of any scholar, but scientists seem much more willing to look under rocks.
Blind spot thinking is like stretching, and practice makes perfect.
Training yourself to think unthinkable thoughts has advantages beyond the thoughts themselves. It's like stretching. When you stretch before running, you put your body into positions much more extreme than any it will assume during the run. If you can think things so outside the box that they'd make people's hair stand on end, you'll have no trouble with the small trips outside the box that people call innovative.
Like most difficult and important skills, blind spot thinking is as much a science as it is an art form. Let’s consider a few examples of specific blind spots while keeping our eyes towards the general principles that are illustrated by each.
Example 1: Randomness
In “Randomness in Science” I argue that humans are bad at randomness, that we can’t generate it or detect it very well and furthermore that we have a general aversion to it as randomness is fundamentally at odds with the imperative, shared by all evolved organisms, to control one’s environment. Because of this aversion, the region of idea-space that contains randomness-related ideas and solutions is likely under-explored.
There are some things that are easy for us to ignore (or difficult for us to think about) by virtue of our unique evolutionary history as featherless bipeds. This type of blind spot runs deep, an inevitable consequences of the inherent limitations and biases of the human psyche. Being aware of these cognitive blind spots is one thing, but being able to capitalize on it is another—it’s an uphill battle, but if you can battle the hill successfully a treasure may await.
It may always be difficult for humans to look into these blind spots, however there other minds that should have no problem doing so—of course I’m talking about AI—Artificial Intelligence, or, as James Evans calls it, Alien Intelligence. Evans proposes that, “we build machines not merely to substitute for human cognition, but to radically complement it.” In a 2021 paper, “Accelerating science with human versus alien artificial intelligences” Evans illustrates the potential of this approach by showing that predictive models (for material and drug discovery) that incorporate human expertise strongly outperform human-naive models (see paper for details).
From the abstract:
“These models succeed by predicting human predictions and the scientists who will make them. By tuning AI to avoid the crowd, however, it generates scientifically promising "alien" hypotheses unlikely to be imagined or pursued without intervention, not only accelerating but punctuating scientific advance. By identifying and correcting for collective human bias, these models also suggest opportunities to improve human prediction by reformulating science education for discovery.”
From the discussion (emphasis mine):
By identifying and correcting for collective patterns of human attention, formed by field boundaries and institutionalized education, these models complement the contemporary scientific community. A further class of alien predictions could be tuned to compensate not only for emergent bias, but universal cognitive constraints, such as limits on the human capacity to conceive or search through complex combinations (e.g., high-order drug cocktails). Disorienting hypotheses from such a system will not be beautiful, but being inconceivable, they break unbroken ground and sidestep the path dependent “burden of knowledge” where scientific institutions require new advances built upon the old for ratification and support… Our approach can also be used to identify individual and collective biases that limit productive exploration, and suggest opportunities to improve human prediction by reformulating science education for discovery. Insofar as research experiences and relationships condition the questions scientists investigate, education tuned to discovery would conceive of each student as a new experiment, recombining knowledge and opportunity in novel ways.
So what are the take home messages here?
1) Blind spots can arise from “universal cognitive constraints” or “field boundaries and institutionalized education”. The latter kind of blind spot, arising from the constraints/incentives of various institutions/systems is what I am writing about in relation to academic psychology research—see below for examples.
2) Artificial intelligence is uniquely valuable when it is used to complement human intelligence and look into our blind spots. This leads to a vision, “whereby machines and persons recursively combine to augment one another in generating collective intelligence, enhanced knowledge, and other social goods unattainable without each other.” (from another Evans paper, “Social Computing Unhinged”)
3) Education can be reformulated for scientific discovery if we conceive of each student as a unique experiment in the recombination of knowledge and opportunity.
Currently, the vast majority of science students are funneled through educational systems in which the same subjects (biology, chemistry, physics) are taught in the same sequence and students take the same assessments (AP, IB, SAT, etc.) with the goal of getting into the same universities. This amounts to a tremendous homogenization of intellectual diversity; of course some students explore on their own in what little free time they have, but the standardization of curriculum and school structure sets everyone on the same few roads through the landscape of scientific knowledge—it’s as if we are running the same experiment over and over again and hoping to get different results (i.e. the definition of insanity).
An education reformulated for discovery would do the opposite—the goal would be to help each student strike out on their own and develop an idiosyncratic set of knowledge/skills. Want to start specializing in psychology and AI at the age of 12 and only learn other sciences as needed? Sure, go for it. Want to focus on computer science, mathematics, and ecology? Why not, you’ll have a very different mind than most people in the field and perhaps be able to develop new insights because of it.
Example 2: Plant Blindness
There are universal cognitive constraints that limit our interest and appreciation of plants. From Wikipedia:
Plant blindness is an informally-proposed form of cognitive bias, which in its broadest meaning, is a human tendency to ignore plant species. This includes such phenomena as not noticing plants in the surrounding environment, not recognizing the importance of plant life to the whole biosphere and to human affairs, a philosophical view of plants as an inferior form of life to animals and/or the inability to appreciate the unique features or aesthetics of plants.
It’s not hard to see why humans are less likely to perceive plants (they are stationary, similarly coloured, and generally part of the background), but what’s more interesting is that this perceptual bias bubbles up into our higher faculties. It is in this sense that plants may represent a blindspot in our thinking.
Thus, research suggests that priority is given to variable colors, movement, and familiar objects in order to most effectively detect threats and potential food sources. As plants do not often fit this criteria, many scientists think the human brain tends not to fully process their visual presence. Additionally, primates have been shown to have a preference for organisms that behave similarly to their own species. As plants behave very differently than humans, this also suggests that there is an intrinsic component to plant blindness.
Plant blindness is also culturally mediated, and modern western culture is likely only enhancing the blindness.
In societies where plant blindness is prevalent, several cultural mechanisms are considered to contribute to the phenomenon. Zoo-centric education is considered to be one main cause. In the United States, high school biology textbooks devote only 15% of their content to plants. In many societies, there is not thought to be a comprehensive understanding among citizens of the complexity behind plants' behaviors, reactions, and movements. The pervasive misunderstanding of evolution as a linear mechanism where humans are most evolved and plants are least evolved, rather than as a complex, non-hierarchical process, may also cultivate plant blindness. Plant blindness is also partially attributed to increased urbanization, which has led to nature-deficit disorder and the decrease in prominence of plants’ roles in everyday life. Finally, the concept that animals are more important than plants is reinforced through cultural over-representation of animals, such as in mascots.
Why does any of this matter?
Several concerns exist regarding the potential effects of plant blindness. Most notably, plant blindness may lead to less funding being available for plant conservation efforts. Plants make up 57% of the endangered species list, while only 3.86% of funding for endangered species is allotted to them.
Plant blindness is also thought to have led to a deficit in plant science research and education. Plant science research has been defunded, interest in botany majors has decreased, and plant biology courses have been terminated in recent years.
If I were a young biology student (and not a has-been high school biology teacher) this line of thinking might convince me to consider specializing in plant science—something I basically didn’t think about at all when I was younger for reasons that are not clear to me now (but I guess that is the sign of a blind spot). At least one person in the know, Noubar Afeyan, co-founder of Moderna, is of the opinion that it is a fantastic time to get into plant science. From his conversation with Tyler Cowen on the podcast Conversations with Tyler:
COWEN: Plant biotech — overrated or underrated?
AFEYAN: Let me make sure. Say more. Plant biotech as a future potential?
COWEN: As a future potential, say, to protect against climate change.
AFEYAN: Highly underrated.
COWEN: Tell us why.
AFEYAN: Just like we understood very little about human health, we understand even less about plant health. Plant health is manifested in yield and resilience and drought and in the functionality of plants, which we have — other than feeding ourselves with or animals with — done very little else with. The technological capabilities are now absolutely upon us to be able to harness plants and their own ecosystems to do a lot more than just create food, and I think that that’s just the beginning.
We work in this area, so I’m not saying this as a spectator. I think in the 30 years I’ve been involved in biotech, where there was an initial excitement but ended up with Monsanto going down a genetic modification route, that the understanding of plants as living productive systems that can be harnessed to do things, including in climate, is just beginning. I think it’s got a lot of promise.
Example 3: Sports
In “The Future: Where are the Colors and the Sports?” I propose that sports are a significant blind spot in futurist thinking. I won’t recap the full argument because this article is long enough already, but suffice it to say that 1) when we think about the distant future, we exhibit the far mode of thinking and thus are more likely to think about abstract ideals and values, not the “lower” desires and emotions which underlie our interest in sports, and 2) futurists/intellectuals tend not to be the type of people who are very interested in sports and thus are probably underestimating its role in the future.
At their best, athletics improve our physical and mental health and give us an outlet for tribal energies that doesn’t lead to violence. Improving sports and enhancing their positive impact on the world are important goals that are not discussed nearly enough in intellectual/EA/long-termist circles. I welcome more contributions like Applied Divinity Studies’ excellent essay The Transhuman Olympics in which he writes:
“[The Olympics] could be a genuine celebration of human achievement in both athletic, and scientific spheres. Moreover, by leveraging the popularity of the Olympics, we could use athletics as a platform to incentivize and fund the development of improved pharmaceuticals, improved prosthetics, and medicine with general prosocial uses.”
Example 4: Blind Spots in Academic Psychology
Many blind spots arise from the constraints and incentives that we face by virtue of being embedded in a variety of systems and organizations (socio-economic, cultural, religious, political, etc.). The following excerpt from the aforementioned paper about amateurs in psychology illustrates a few of these blind spots; again, even though I am discussing psychology, I think it should be clear that these blind spots apply to all sciences and many aspects of culture.
We propose that amateur psychologists can most effectively improve knowledge diversity in PBS (psychological and behavioral sciences) if they focus on “blind spots”—endeavors that are neglected in academia (e.g., because they are not incentivized, or due to some other constraints) but have a large potential to lead to new insights and discoveries.
Blind spot 1: long-term research
For example, the “slow scholarship” movement highlights how scholars face a general intensification in the pace of work and an increasing pressure to publish (Harland, 2016; Hartman & Darab, 2012). Research indicates that the average number of publications at time of hiring for science faculty positions has been steadily rising in recent years) (Pennycook & Thompson, 2018; Reinero, 2019; Van Dijk, Manor, & Carey, 2014); trends like this may influence researchers, especially early career researchers, away from projects that require dedication over a long period of time. This suggests that long-term research projects are generally a neglected area in academia and amateurs could do valuable work by focusing their efforts in that way. This may involve spending decades to build rich and multilayered psychological theories, investigating psychological phenomena in greater detail, etc.
Comment: When everything seems to be zigging towards speed, efficiency, and instant gratification, doing something that takes a long time is the ultimate zag, a kind of meta-blind spot. The challenge is getting yourself to do something for an extended period of time when the payoff is uncertain and the positive reinforcement is sparse or non-existent. This is when a deeper sense of meaning and purpose (the kind you can get from personal tragedy or religion for example) can help us persevere through the tough times. I have many thoughts on this, but that’s a topic for another time.
“Make your own Bible. Select and collect all the words and sentences that in all your readings have been to you like the blast of a trumpet.” ― Ralph Waldo Emerson
Blindspot 2: basic observational research
Given that academic psychology emphasizes experimental research, perhaps to the exclusion of basic observational work (Muthukrishna & Henrich 2019; Rozin, 2007; Rozin, 2009), amateurs could make contributions by conducting observational studies that aim to identify new phenomena or characterize the generalizability of already known phenomena. In particular, amateurs with access to non-WEIRD populations, niche subcultures, unusual datasets, or unique environments may be able to provide novel observations. These observations could then either guide their own theoretical ideas and independent research, or they could be used to inform academic psychologists about what their work is potentially missing or to inspire new academic research.
Blindspot 3: speculation
Another scientific activity which amateurs could focus on is speculation, which has played a crucial role in many scientific discoveries (Achinstein, 2018; Stauffer, 1957). In some cases, scholars were forced to speculate about phenomena that could not yet be empirically investigated due to methodological limitations, and these speculations then guided the research once the methodology became sufficiently advanced (Koyré, 2013). In other cases, unrestrained speculation beyond the available scientific evidence led to new insights that inspired research and produced novel discoveries (Stauffer, 1957). However, modern scientific norms and the general focus on experimental research discourage professional scientists from discussing or publishing some of their wilder speculations (Bunge, 1983; Panchin, Tuzhikov, & Panchin, 2014; Starokadomskyy, 2015; Swedberg, 2018). Free from these norms, amateurs could work to collect, organize, and publish their own speculations or those of professional collaborators. Given the accessible subject matter of psychology, it is not unreasonable to think that laymen could provide valuable insights.
Blind spot 4: aimlessness
Academic researchers are also disincentivized from pursuing projects that are more “aimless” in nature, which means they do not have planned outcomes or predetermined goals and arise from intrinsically enjoyable activity that is not necessarily goal-oriented (Clark, 2018; Friston et al., 2017). Such projects may involve simply collecting observations and thoughts about human behavior or mental processes out of interest, but these observations and ideas may over time naturally grow into theories, research projects, and other endeavors that can enrich psychological knowledge. Aimless projects may suffer from a “failure to launch” problem in that it will be difficult for academic researchers to justify devoting significant time and resources to projects that do not have a clear focus or sell in the very initial stages. On the other hand, amateurs would not face these constraints and would be able to “play” with different ideas and observations to explore where this can take them.
Comment: In any competitive field like science, it is very hard for people to justify spending significant energy and time on anything that isn’t nearly guaranteed to yield quantifiable, resume-ready accomplishments—they don’t say “publish or perish” for no reason. I’m certainly not saying it’s easy, but if you can resist the constant pressure to be “productive” and “busy” and find ways to be more aimless, you might have a better chance of finding the Next Big Thing (whatever that is to you). This strategy seemed to work for many great thinkers - Darwin was a Slacker and You Should be Too.
(shameless plug: Seeds of Science, a journal specializing in speculation and non-traditional scientific writing, that I co-founded with the co-author of this paper)
Blind spot 5: interdisciplinary research
Academic researchers are disincentivized from pursuing interdisciplinary research. The disciplinary structure of many universities, funding bodies, journals, and professional organizations makes it more difficult to procure funding, publish, and receive recognition for research that does not neatly fit into one discipline (Bark, Kragt, & Robson, 2016; Bromham, Dinnage, & Hua, 2016; Campbell, 2005; Lamont, Mallard, & Guetzkow, 2006; Uzzi et al., 2013; Yegros-Yegros, Rafols, & D’este, 2015). In addition to these structural challenges, there are social and attitudinal barriers that may dissuade academics from conducting interdisciplinary research (Campbell, 2005; Macleod, 2018; Morse et al., 2007; Siedlok & Hibbert, 2014). Differences in expertise, jargon, and norms between disciplines make it challenging for a researcher to do individual or even collaborative work outside their field (Campbell, 2005; Cummings & Kiesler, 2008; Macleod, 2018; Morse et al., 2007; Siedlok & Hibbert, 2014). Potential interdisciplinary researchers may also face the loss of credibility that comes from not being an expert in one particular field (the “expert’s dilemma”) (Yanai & Lercher, 2020). Amateur researchers are more likely to either not be subject to these challenges (e.g., they may not be pursuing funding) or not care about them (e.g., they may not be as concerned with credibility or how they fit into the academic job market) and thus are free to pursue interdisciplinary projects in a way that academics are not.
Blindspot 6: uncommon research areas
Amateurs can also make research contributions by focusing on uncommon research areas that are neglected for some reason. These research areas may be outside the realm of hot topics (Rozin, 2007) that can lead to many citations and therefore advance one’s career, they may be a taboo, or they may represent something that is generally not associated with academic psychologists (e.g., religious behavior) (Bloom, 2012; Norenzayan, 2016; Rozin, 2007). There are also some subjects that may be inherently difficult to study because they require considerable domain-specific knowledge (e.g., high-level athletic performance, hunting or survival skills, extensive meditation practice) which a professional researcher is unlikely to have. Collaboration with amateurs who have special knowledge or abilities could provide unique insights into these areas.
One question that I find useful for blind spot thinking: what current idea or practice will people 100 years from now (200 years, 500 years, etc.) look back on and think was absolutely insane in the same way that we look at some of the ideas/practices from the past? Do we have taboos that will seem laughable in the future? Will they have taboos that seem unthinkable to us now?
The blind spot section of the amateur psychology article (and this essay) concludes with the following paragraph:
Taken together, this discussion highlights one general area in “research-space” that may be especially promising: long, aimless, speculative, and interdisciplinary research on uncommon or taboo subjects. Again, although not in PBS, we might hold up Charles Darwin as an exemplar. While Darwin eventually did become a renowned professional scientist, at the time of his departure on the HMS Beagle in 1831 he was very much an amateur, a 22-year-old with no advanced degree or publications to his name who had to pay his own way on the voyage (Bowlby, 1990; Keynes & Darwin, 2001). Darwin’s work on evolution certainly took a long time to develop (the Beagle’s voyage took 5 years and he did not publish On the Origin of Species until 23 years after he returned). It was aimless in the sense that he did not set out from the beginning to develop a theory of evolution. His work was highly interdisciplinary (Darwin drew on numerous fields within the biological sciences in addition to geology and economics), was the culmination of a huge amount of basic observational work, and was not necessarily an experimental contribution (though he did make those as well), but primarily theoretical (and sometimes more speculative) in nature. Darwin’s theories were taboo in the sense that they went against the prevailing theological ideas of the time and caused significant controversy (and still do). We speculate that there may one day be a Charles Darwin of the mind who follows a similar path and hope that this paper provides the smallest nudge in this direction.
Is the Charles Darwin of the Mind reading this right now?
The picture at the top of the article is of the sculpture “Karma” by Do-Ho Su, located at the New Orleans Museum of Art. Here are some more pictures:
I would add that the landscape of good and bad ideas is always defined by a function that evaluates ideas as good or bad. It is important because otherwise it might be thought that the landscape of ideas is a piece of the objective truth which it isn't.