Where do questions come from?
(Commonly attributed to Asimov, though I haven't yet found a credible citation)
As I argued in my previous post, the
questions that animate science must make the erotetic cut, but this is only a necessary condition. We still need to answer the question, "where do such questions come from?"
As with scientific R&D in general, there is nothing uniquely
scientific about asking questions. Humans being creatures endowed with an insatiable
thirst for understanding, we are (or seem to be) predisposed to fixate on our points of confusion and gaps in knowledge as we encounter them. Ultimately, this is where the questions that
animate science come from, though not all such questions are well-suited to
observational scrutiny. As I have previously mentioned, if an idea cannot be
held accountable to observation, then we are not doing science, and this applies specifically to the ideas we offer in answer to our questions, and by extension to the questions, themselves. In this post, I will narrow my focus (for the most part) to those questions and answers that are amenable to observational scrutiny.
The
questions that animate science tend to come from either of two directions, a
fact that probably does not seem noteworthy until I tell you that it is the source of a surprising amount of conflict within the scientific community.
I’ll get to the conflict in a bit, but it would be helpful if we first
understand what these two approaches are.
I will call them observation-driven inquiry and theory-driven inquiry.
Observation-driven
inquiry begins with curious patterns detected in observational data, characteristics about some
dimension of reality that we have described and that seem unique or that make us wonder why they aren't some other way instead. That the world is working in some way is made clear by such observation, but exactly how it worked to that end remains to be determined.
For example, over the course of the last two and a half or three centuries,
the global population, as well as the regional and local sub-populations that it
comprises, have been undergoing a transition from a regime characterized by
high mortality and high fertility rates to one characterized by low mortality
and low fertility rates. Furthermore, a lag in time
between the mortality and fertility transitions has driven the explosive
population growth that has led to our current world population of 7,000,000,000+, though fortunately this explosive growth seems to be on the
decline and there is at least a hope that growth will level off by the end of
this century. Taken together, these
trends in fertility, mortality, and population growth are known as the
Demographic Transition (or DT for short).
The changes in the global population size and age structure that these changes have entailed present us with pressing concerns for the sustainability of our current social, political, economic, and medical systems, so we are compelled to understand the factors that have driven and continue to drive changes in growth rates, in other words factors that drive changes in fertility and mortality rates. The DT thus poses a
pressing target for understanding; it raises questions like, why have these mortality and fertility
transitions unfolded in the way that they have? and what are the circumstances under which such changes are likely to
occur, in which direction, and to what social, political, economic, and/or medical effect? Demographers have been
trying to answer these questions since the early Twentieth Century, with
early guesses emphasizing Neoclassical economic principles, later ideas
stressing the diffusion of cultural norms from centers of development to
developing regions, and a plurality of current answers hybridizing various
aspects of previous perspectives. At the
same time, we have collected better demographic data from many areas of the
world that were not originally available to the early DT researchers, and of
course new data continue to come in as the ongoing population dynamics of the
world have continued to unfold, meaning that the explanatory target of DT research has shifted around a
bit since its inception.
A second
example comes from geology, regarding the extent and causes of what may have been our planet’s most dramatic ice age, the late Proterozoic Ice Age. Beginning in the late Nineteenth Century, a
series of distinctive geological deposits known as late Neoproterozoic Glacial
Deposits (LNGDs) have been discovered on every continent, suggesting that
virtually all of the Earth’s terrestrial surfaces, including in the temperate
and tropical latitudes, were once covered by extensive ice sheets sometime
between approximately 850 million and 635 million years ago. Since that time, our planet has not experienced such extensive
glaciation, making it all the more noteworthy. The question thus rises, what unique set of factors came together to lead to such an
unparalleled ice age, and could it happen again? As with DT research, a number of competing explanations have been
offered for this ice age ever since it was discovered in the mid 20th century. One family of explanations emphasizes the interaction between changes in the Earth’s orbit around the Sun and the tilt
of its axis, which could have decreased and changed the daily and annual intensity
of solar radiation reaching the Earth's surface, potentially allowing for the formation and expansion of continental ice
sheets. Alternatively, the “Snowball
Earth Hypothesis” suggests that a phenomenon called “albedo,” referring to the reflection of the sun by white surfaces, led to a process of positive feedback in which the initial formation of continental
ice sheets in the tropics acted to deflect sunlight, leading to further global cooling and allowing
for the formation of even more extensive ice sheets. In this scenario, the runaway albedo effect propagated to such a degree that even the oceans were covered by a sheet of ice
(hence the label “Snowball Earth”), or at least that they were globally slushy (“Slushball Earth”). The jury
is still out on the most credible answer to this question, though at present the Snowball Earth hypothesis is faring much better than the orbital hypotheses in the debate, as I understand it.
Unlike observation-driven inquiry, theory-driven inquiry begins with a prior belief already in mind about the way that some aspect of the world works. In this case, questions arise particularly
when such prior understandings run into observations that seem to contradict then. The critical word here is seem, because many seeming
contradictions turn out to be mere paradoxes – seemingly contradictory statements that may nonetheless be true – upon further examination. In the case of a paradox (but not a true contradiction), the root of confusion typically lies in a flaw or a gap in our own understanding
rather than a true mismatch between the two statements in question. The goal of theory-driven research is then to come up with a solution to the puzzle that accommodates for the seeming incongruity between prior understanding and new observation, in other words by showing that the seemingly contradictory observation does not in fact violate the prior understanding. The effect of such accommodation is that the newly observed reality
is neatly subsumed under the prior belief.
For example,
Neo-Darwinian theory (which synthesizes Darwin’s theory of natural selection
with modern genetics) asserts that biological traits (anatomical,
physiological, or behavioral) are not expected to emerge or persist in a species that would act to
undercut the fitness of individual organisms within that species, i.e. that would undermine their ability
to “leave more surviving offspring or more copies of their genes” (John Alcock,
The Triumph of Sociobiology, p. 32). Alcock continues on to say that
“This is a theoretical perspective, and like all useful theories, it shapes the expectations of observers in productive ways, so that they can first identify the surprising features of nature and then develop testable hypotheses to account for these surprises. Someone who understands Darwinian theory is prepared to be puzzled by certain things, not others.”
For example,
the emergence and persistence of altruistic behaviors in various highly social species,
including social insects, group-living mammals, and others besides, have provided one of the major
puzzles for sociobiological research (the area of Darwinian evolutionary biology
devoted to the study of the evolution of social behavior). If individuals are designed by natural selection to promote the reproduction of their genes into the future, why would an individual ever invest one's own time, energy, or resources toward the well-being of another individual at the expense of one's own?
Scientists
who are accustomed to approaching research from the angle of
observation-driven inquiry often regard the theory-driven approach with considerable
suspicion because, at first impression, it seems to embody a rather non-scientific
approach to establishing belief. Making accommodations for seeming contradictions is the business of apologists, defenders of the faith, not scientists, because such behavior short-circuits the definitively scientific act of endangering ideas. Or does it?
As it turns out, this approach is nowhere near as unscientific as it may initially appear. First, as advocates of the theory-driven approach would counter, successfully demonstrating that new observations continue to fall within the boundaries set on reality by old understandings speaks volumes for the continued value of those understandings in helping us to make better sense of our world. Second and more importantly, researchers dedicated to this approach will often be the first to admit that their success in accommodating for the paradoxical is dependent on a goodness of fit between their accommodation and further rounds of observational scrutiny. In other words, the accommodation that resolves the paradox and subsumes observation under prior understanding is itself treated as a testable hypothesis, and not all such accommodations will stand up to scrutiny.
As it turns out, this approach is nowhere near as unscientific as it may initially appear. First, as advocates of the theory-driven approach would counter, successfully demonstrating that new observations continue to fall within the boundaries set on reality by old understandings speaks volumes for the continued value of those understandings in helping us to make better sense of our world. Second and more importantly, researchers dedicated to this approach will often be the first to admit that their success in accommodating for the paradoxical is dependent on a goodness of fit between their accommodation and further rounds of observational scrutiny. In other words, the accommodation that resolves the paradox and subsumes observation under prior understanding is itself treated as a testable hypothesis, and not all such accommodations will stand up to scrutiny.
Nor are all approaches
to theory-driven inquiry so monopolistic in trying to subsume new observations under the coverage of a single understanding.
Evolutionary biologists, for example, readily concede that there are
other evolutionary processes beside natural selection that can explain changes in the frequency of genes or biological traits within a species, including changes
that either reduce reproductive fitness or are selectively neutral. Thus, sometimes the solution to a Darwinian puzzle requires no special intellectual contortion to resolve a paradox but instead draws upon other, non-selective theories about evolutionary processes. On this point,
evolutionary biologists distinguish between four “forces” of evolution –
mutation, selection, gene flow, and genetic drift – and further distinguish
between different kinds of selection (natural, sexual, group, artificial), all of which are expected to operate under different sets of circumstances.
A similar
situation holds in medicine and public health regarding the cause of
diseases. One of the most revolutionary intellectual developments in
medicine over the last three or more centuries was the introduction of what we
now call the germ theory of disease.
This idea suggests that many diseases are caused by infection by small
critters (i.e., “germs”) like prions, viruses, bacteria, protozoa, fungi, and
arthropods (worms, arachnids, insects), which parasitize the body of their
hosts for their own purposes, and to the detriment of the host’s regular
biofunctions. With the emergence of
microbiology, parasitology, and immunology, our ability to demonstrate the presence and adverse activities of
such pathogens has revolutionized our ability to understand the source of many diseases, and to treat them…
…But not all of them. While our understanding of many diseases has improved considerably because of the germ theory of disease, this in no way changes that fact that a good number more of
diseases are instead caused by genetic defects (e.g., sickle cell anemia, Tay-Sachs
disease), developmental mistakes during fetal development, or exposure to
various detrimental substances throughout life (smoke, smog, sugar, salt, saturated fats, carcinogens, poisons, allergens, etc.). For this reason, pathologists and epidemiologists have hardly given up on alternative
explanations of disease, just as most evolutionary biologists have not given up
on genetic drift, gene flow, and mutation as drivers of evolution alongside the
incredibly powerful concept of selection.
So, we might further subdivide theory-driven inquiry into two subcategories: (1) accommodation-driven
inquiry, which attempts to subsume puzzling phenomena under prior understandings by
showing them to be mere paradoxes, and (2) a “which theory is better?” approach, which
attempts to identify which out of a set of prior understandings fits best with a given
observation. In fact, this second
approach comes very close to the observation-driven mode of inquiry I described
above. For example, in their efforts to
understand the climatic mechanisms that drove the late Neoproterozoic Ice Age, geologists did not simply make up new ideas to fill this gap. Instead, they went to one of two prior understandings of glaciation, each having much broader applicability than just to the ice age in question.
Explanations that emphasize orbital parameters go back to the work of the early Twentieth Century Serbian scientist Milutin
Milanković, whose ideas predated the discovery of the Neoproterozoic Ice Age and are still held in high esteem regarding the cycling of episodes of glaciation and deglaciation during the Pleistocene epoch (from
approximately 1.8 million to approximate 12 thousand years ago). Conversely, the concept of a runaway albedo
effect, which serves as the backbone of the Snowball Earth hypothesis offered
by Joe Kirschvink in 1992, was originally envisioned by the Russian
climatologist Mikhail Budyko in the 1960s, who saw such runaway albedo only as
an extreme and unlikely special case of a more general model of albedo that he developed.
So perhaps there isn’t such a huge difference between observation-driven
and theory-driven researchers after all, at least not in every case.
This brings us
to the contentious topic of ‘theory.’ As
many readers are probably aware, evolutionary biologists, climate scientists, and their respective sympathizers
frequently butt heads with unbelievers over the meaning of the word ‘theory’ (among
other things), particularly when it comes to dismissive expressions like “evolution
is just a theory.” Unfortunately for everyone involved in the debate, in
common usage, ‘theory’ has the meaning ‘untested idea,’ making it synonymous
with ‘conjecture,’ ‘speculation,’ ‘guess,’ ‘hunch,’ or “something you dreamt up after being drunk all night” (another quote commonly attributed to Asimov) ... not that guesses have no place in science. Thus, to assert that evolution is just a theory is to assert that it is a baseless speculation, and only one among many
alternative ideas about the nature of life on Earth, at that. The rehearsed response of scientists is to counter that ‘theory’ stands out from hypotheses not because theories are untested hypotheses but on the contrary because they are exceptionally well-tested and observationally well-supported hypotheses. Thus, in scientific jargon, calling an idea a 'theory' is high praise, synonymous with 'knowledge,' not a dismissal.
But the
story is a little more complicated than scientists usually let on, because in fact we use ‘theory’
in two different ways (a poorly recognized fact that unfortunately creates the
potential for the related fallacies of equivocation and amphiboly; see also here and here). The first sense of ‘theory’ is the one just defined,
referring to a well-supported hypothesis, standing as the result (i.e., the end) of a research cycle. The second sense of ‘theory’ is the one discussed
earlier, referring to a prior understanding, well-supported or otherwise, that functions not to finalize research but to catalyze it. In this case the theory is not directly tested or testable, only the accommodations that are intended to link it to observation. This meaning of ‘theory’ comes much closer to the meaning intended when
we say “the theory of evolution through natural selection,” “the germ theory of
disease,” or “theoretical physics.”
Effectively,
what these research-orienting theories do is provide a generic framework for stories that we might tell in our efforts to account for whatever phenomena we hope to
explain. These theories are deliberately
vague in detail, asserting only a broad outline about explanations of mysterious phenomena. For example, while the germ
theory of disease tells a generic story about the invasion of host organisms by
smaller organisms that then prey upon the host, causing all kinds of
health problems for the host in the process (i.e., the dis-ease), the theory remains deliberately silent
regarding the particular details of such infections. This vagueness is the secret to
the theory’s success, because as it turns out, there are many different kinds
of infectious pathogen (prions, viruses, bacteria, protozoa, fungi, and
arthropods), each relying on different routes of introduction into the host
body and exploiting the host body in different ways, leading to different
health outcomes: acute vs. chronic disease; nausea vs. pain vs. fever; mild illness vs. fatality; etc.
At face
value, the untestability of this kind of theory may seem like a huge liability for productive debate between different
communities of belief, at least when one or more of the theory's components and the questions it generates are disputed. As I
suggested in my previous post, asking any question that assumes any reality
that the audience is unwilling to accept creates the problem of the loaded question. Despite this seeming liability, however, I doubt that
things are so bleak, for two related reasons:
First, many of the theories that underlie the questions that scientists ask turn out to have huge utility. For example, in the case of the germ theory
of disease, our ability to identify the infectious pathogens that cause many of the epidemic diseases we have suffered for millennia has empowered us to significantly reduce their future potential, owing to various public health measures (improved hygiene, sanitation programs, and vaccination) that interfere with the life cycle and transmission of these infectious pathogens. (It's an important component of the mortality transition that led to the DT described above, incidentally.) When questions and answers founded on 'absurd' concepts prove to be so eminently successful, it becomes increasingly difficult to consider them absurd any longer.
Second, while such theories are too
vague to be scrutinized themselves, it is still quite damning when researchers who
are dedicated to them prove unable to fit them to observations. A track record of failed accommodation after
failed accommodation constitutes its own sort of endangerment, even if it is a bit slower in the unfolding and not quite
the same as falsification. So, we have a sticky situation in which our assumptions both color our research and are challenged by it, a fact that I don't think Steven Novella would much care for:
(Of course, stubborn advocates of a failing theory might also continue to maintain that the apparent shortcoming of their theory is due to a lack of talent on their own part, not on any deficiency of the theory; these are the ones who are most deserving of Novella's censure, I think.)
(Of course, stubborn advocates of a failing theory might also continue to maintain that the apparent shortcoming of their theory is due to a lack of talent on their own part, not on any deficiency of the theory; these are the ones who are most deserving of Novella's censure, I think.)
Asking important questions, and asking impossible questions
Even out of those questions that we do ask, we do not approach them all with equal rigor. We do triage, because we know that we cannot possibly address them all with the meticulous scrutiny necessary to either dismantle them or establish them as standing knowledge.
Needless to say, the importance of beliefs in general, the importance of questions, and the importance of answers to such questions, are highly subjective judgments. The smugness of scientists about their own discipline often goes part and parcel with the sense that scientists working in other disciplines are wasting their time on topics of trivial importance, though fortunately this smugness is often counterbalanced in the opposite direction. I prefer to assume that other sciences are as fascinating as the ones I spend most of my time in (anthropology, demography), and I have a short list of other disciplines that I would pursue with enthusiasm if only I had a few more lifetimes to live. Stepping out of the scientist vs. scientist dynamic, the opinions of the general public toward what questions are important to ask are even more variable, as are their opinions of everything else, because let's face it: the "general public" is a pretty huge and heterogeneous entity.
Subjective though such judgments may be, scientists are nevertheless obliged to justify our research to others, especially to funding agencies and to the professional journals whose choice it is to publish our work. For example, grant proposals submitted to the United States' National Science Foundation (NSF) require that a section of the proposal be dedicated to the discussion of intellectual merits and broader impacts of the research proposed. Not surprisingly, the promise of economic, social, political, and/or health benefits for the American public favors the funding of such research, whereas replication research is too rarely funded. There is also a cottage industry of op-ed pieces offering lists of what different authors believe to be the most pressing questions in need of answer (for example this two-part blog series from NPR, here and here).
By the same token, there is frequent discussion (and debate) about which questions can be answered by science and which remain out of its grasp, such as is reflected in Robert Krulwich's NPR blog post here. This question frustrates me because it glosses over two very different constraints on science, one of which is considerably more fundamental than the other. The first and more fundamental constraint is that no question can be considered scientific if provisional answers cannot be subjected to observational scrutiny. There is nothing really profound here, however, only the recognition that hunches that are not endangered are just hunches. Moreover, whether there are good answers to questions (the right ones, even) that cannot be tested is the great unknown; how would you ever know whether an answer to a question is untestable simply because you have not yet found a way to test it? elusive as such knowledge may be, there are some questions that seem on the face of it to be too broad, too generally stated, or too vague to be approached scientifically, for example most of the questions in the aforementioned NPR blog series about the "20 most important questions." Instead, the sorts of questions that are actually scientifically approachable tend to be very topical (e.g., this "to-do list" for Parkinson's researchers), which unfortunately tends to sacrifice importance, or at least breadth of coverage, for specificity and operability.
The second constraint is the possibility that some phenomena of the world elude principled behavior. In this case, no conjectural answer that purports to understand it will ever be correct, exactly because no understanding is possible. but once again, even if such an impossibility were true, we would never know it, because our ability to put bad ideas on the table before we find good ones is no proof of the impossibility of good ones overall. Many human scientists (anthropologists, psychologists, sociologists, economists, and political scientists) continue to seek better understandings of human nature, this in spite of the alternative possibility that no such understanding is possible because we don't make any sense, because we are endowed with a crazy little thing called free will (one could call it "human anti-nature"). Responsible scientists should be comfortable conceding that we can never really know if a given aspect of the world eludes understanding. At the same time, few of us will stop seeking possible and testable answers to our questions, and when we stumble upon good ones, in other words ones that stand up to honest observational scrutiny, we will feel vindicated, full well knowing that these may be displaced by even better answers later on down the line. As a matter of course, we approach no phenomenon as if it cannot be better understood.
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