Hokum's Razor (Scientific R&D, Part 2.1.2)

"Nature ... is not always noted for its parsimony." - Donald A. Dewsbury

In this post, I want to follow up on my previous comments regarding simplicity and the dubious role it plays in the unificationist agenda for science.  At no point in that discussion did I refer to Occam's razor (or the Law of Parsimony, as it is sometimes called), and this was a peculiar oversight on my part given its central place in the unificationist playbook.  In fact, while few unificationists would ever explicitly identify themselves as such (the label being more of a shorthand used by philosophers of science),  the majority will almost certainly invoke Occam's razor at some point in their career, so much so that it has become a standard fixture in the dramatic depiction of science-types (or their adversaries) in popular drama, due in large part to the success of the film adaptation of Carl Sagan's Contact.  Noteworthy mentions since then include The X-Files (Season 8, Episode 4, "Patience"), Scrubs (Season 7, Episode 1, "My Own Worst Enemy"), House M.D. (Season 1, Episode 3, "Occam's Razor"), and The Big Bang Theory (Season 1, Episode 9, "The Cooper-Hofstadter Polarization").

Okay, so what is this rule?  This is a deceptively simple question, as I intend to demonstrate, but in a nutshell, it is the application of the principle of economy ("never do for more what you can do for less") to explanatory matters: "Plurality [in explanation] should never be posited unnecessarily."  The rule takes its name from the 12th Century philosopher William of Ockham, though he was hardly the first to suggest it; it can be traced back to influential Hellenistic philosophers like Aristotle and Ptolemy, and variants of the rule were in wide circulation during Ockham's time, as well.

Since then, several well-known figures in science have given expression to the rule, or at least to rules that resemble it.  This includes Isaac Newton's "we are to admit no more causes of natural things than such as are both true and sufficient to explain their appearances," Ernst Mach's "scientists must use the simplest means of arriving at their results and exclude everything not perceived by the senses," and of course the Einsteinian pseudepigrapha that "everything should be made as simple as possible, but not simpler."  It also includes various expressions of the tenet that "extraordinary claims require extraordinary evidence," made popular (once again) by Carl Sagan (Cosmos, Episode 12, "Encyclopedia Galactica").

At face value, the proliferation of paraphrases of the rule in both academic and popular media might be taken as an indicator of the rule's power and centrality in scientific practice.  Careful consideration of their wording, however, betrays a considerable degree of conceptual disparity between them, worthy of further consideration:

• While some versions of the rule focus on the number of "moving parts" included in the causal account, others focus instead on the plausibility or credibility of these parts regardless of number (Newton's "admission of causes that are true"; Mach's "exclusion of everything not perceived by the senses").  Some articulations of the rule dodge such considerations simply by insisting on the "simplest" explanation.
• Among the versions of the rule that focus on the plausibility or credibility of the cause, these vary between expressions that treat "credibility" as if sharply divided between known and unknown (e.g., Newton's "admission of causes that are true") and those that are relatively more liberal in their allowance for a range of confidences in the truth of various claims.  The fictional and ever-entertaining Dr. House ascribes to the latter: "Why is one simpler than two?  It's lower, it's lonelier, but is it simpler?  Each one of these conditions is about a thousand to one shot.  That means that any two of them happening at the same time is a million to one shot.  [Dr.] Chase says the cardiac infection is a ten million to one shot, which makes my idea ten times better than yours."  In other words, any explanation involving a joint probability of two relatively uncommon conditions is still vastly superior to one involving a single probability of an incredibly rare condition, or in the words of Dr. Cox, "if you hear hoof beats, you just go ahead and think 'horseys'" (unless, of course, you happen to live in zebra country):

• The tenet that "extraordinary claims require extraordinary evidence" is also an extension of this perspective, because our sense of a claim's plausibility is subject to change as new information comes in, though not by much unless the information is strongly in the opposite direction of prior belief.
• While some versions of the rule assert that adherence is more likely to yield correct explanations, or even that contrary explanations cannot be true, others simply assert that such adherence is "better" without saying why, and yet others dispense entirely with the effort to justify adherence.
• Only a few versions suggest that the process of simplification can be taken too far.  For example, Okham's "do not posit unnecessarily" suggests that some degree of plurality in explanation is desirable.  Similarly, the pseudo-Einsteinian "but not simpler" suggests that oversimplification is just as grave a mistake as is needless complexity.
• A careful reading of Newton's version of the rule reveals that it is not concerned with efficiency at all but instead with the plausibility and sufficiency of the causal account on offer; if the posited causes are unlikely to produce the effect in question, or if their truth is in doubt, then the account fails no matter how many or few are suggested.

Deeper into the quagmire of Occam's ambiguous rule

In scientific practice, alleged adherence to the rule likewise masks multiple, qualitatively distinct practices.  To illustrate what I mean, I introduce to you one of the tools that logicians use to evaluate the validity of certain kinds of arguments.  The tool of which I speak is known as 'predicate logic,' and it belongs to a larger logician's toolkit, 'symbolic logic,' which is similar to symbolic algebra in that both describe relationships between variables of unspecified value by combining letters (representing the variable under investigation) and operators (representing their relationships), according to specific rules constraining their possible combinations.

Predicate logic is made up of elements that take the form 'Px', where x stands for the subject of a proposition and P stands for the predicate of the proposition (i.e., the part of the sentence describing the subject; essentially Px means "x is P").  When it comes to formulating expressions in predicate logic that adequately capture the conceptual structure of explanations, we need to combine statements about some earlier, causal condition - something like Cx - with statements about some later, outcome condition or effect - something like Ex.  Specifically, we can combine such statements in one of three possible conditional statements.  (Conditional statements relate two statements in an "if, then" manner).  However, choosing the right combination to accurately convey our causal concept takes some careful consideration.  These are the three candidates:

1. Cx → Ex:  "if situation x exhibits condition C, then it will exhibit condition E."
2. Ex → Cx:  "if situation x exhibits condition E, then it will exhibit condition C" (or in other words, "only if situation x exhibits condition C will it exhibit condition E").
3. Cx ↔ Ex:  "if and only if situation x exhibits condition C will it exhibit condition E" (or vice versa).

The first statement establishes a characteristic outcome-state for situation x, E, given that it previously exhibited condition C.  In this formulation, Cx is identified as a 'sufficient condition' for Ex to be true, and this is very different from an alternative and rather vacuous statement

• Cx → (Ex ˅ ~Ex):  "if situation x exhibits condition C, then it will either exhibit condition E, or it won't."

The second statement, on the other hand, gives condition C exclusive access to condition E: if we see that condition E characterizes situation x, then situation x must formerly have been characterized by condition C.  In this formulation, Cx is identified as a necessary condition for Ex to be true (if Cx is not true, then neither is Ex).  Finally, the third statement, known as a biconditional statement, establishes a doubly exclusive relationship between C and E, such that Cx is both a necessary and sufficient condition for Ex.

The first inferential activity masquerading as Occam's razor involves favoring Cx as both a necessary and sufficient condition for Ex, in other words favoring the biconditional formulation above.  If we attach an index to C in order to distinguish between alternative, mutually exclusive causal accounts, C_ix, where 'i' is a placeholder for a specific C, then the statement "C₁x ↔ Ex" precludes alternative conditional statements linking C₂x to Ex.  In other words, if it is true that situation x will exhibit condition E if and only if it had previously exhibited condition C₁, then it is false that situation x had previously exhibited some alternative condition C₂.

All of the above formulations, however, apply only to a single subject, the situation symbolized x.  If a researcher wishes to expand the scope of their explanation using predicate logic to cover a set rather than a single subject, one of two additional statements is added:

• (x)( ... ):  "for every x, ...," where the ellipsis within the second set of parentheses is a placeholder for a logical statement (for example any of the three formulated above).
• (Ǝx)( ... ):  "for some x, ..."

Each of these formalities, known as the 'universal quantifier' and 'existential quantifier,' respectively, is used to extend the coverage of the statement within the second set of parentheses to a whole set of subjects, either the more inclusive "every x" when using the universal quantifier, or the more exclusive "some x" when using the existential quantifier.

Applying the universal quantifier to the third, biconditional, formulation above is the second practice masquerading as Occam's razor: "(x)(C₁x ↔ Ex)", in other words "It is true of every situation that, if and only if it exhibits condition C₁, it will exhibit condition E."  In doing so, the researcher relieves him or herself of the need to consider novel causes for each newly described instance of Ex, since C₁x is both necessary and sufficient in every situation.  In effect, this formulation globalizes the relationship between E and C₁, making a general principle or law of it and transforming subsequent explanations of C₁x into a highly redundant operation.

The next two practices subsumed under the heading of Occam's razor involve (1) the expansion of condition E to include multiple, qualitatively distinct effects, and (2) the suppression of condition C to include as few separate causal terms as possible:

• (x)(C₁x ↔ (E₁x ∙ E₂x)):  "it is true of every situation that, if and only if it exhibits condition C₁, it will exhibit both condition E₁ and E₂ (and E₃ and ...)."
• (x)(C₁x ∙ C₂x) ↔ Ex):  "it is true of every situation that, if and only if it exhibits conditions C₁ and C₂, it will exhibit condition E.

The first of these practices exhibits the same sort of economy as does killing two birds with one stone; it reduces the need to engage in novel explanatory efforts for every new phenomenon encountered.  The second of these practices, on the other hand, is a formalization of the "minimal moving parts" imperative discussed above.

Abstraction, the fifth and final Ockhamian practice, involves expressing C and E in such a way that some degree of variation around an ideal is tolerated: "situation x exhibits something like condition C" or "situation x exhibits a condition similar to E."  Inclusive expressions like these allow researchers to capture a significantly wider range of individual cases under their explanatory account than can a more rigid expression that demands an exact resemblance between them.  Abstraction, in other words, allows researchers to pigeonhole nonidentical cases into lawful conformity, further reducing the need to produce novel explanations for every new case.

Some examples of Occam's ambiguous razor in the historical sciences

While Occam's razor is frequently treated as if axiomatically true and invoked to legitimate one or two of these practices at a time, it is rare to encounter a researcher ambitious enough to attempt all five at once.  One exceptional example comes from archaeology (my home discipline): British archaeologist Colin Renfrew's explanation of the language geography of our modern world.

In several regions across the globe, clusters of languages bearing close affinities to one another enjoy wide geographic distribution.  For example, the Indo-European languages (e.g., Hindi, Farsi, the Baltic, Slavic, Germanic, Celtic, Hellenic, and Romance languages) dominate the European linguistic landscape, as well as significant areas of Iran, Pakistan, Afghanistan, and India.  Historical linguists have long argued that the shared traits characterizing many of these language clusters exist as a dwindling legacy of a shared linguistic ancestry, for example "Proto-Indo-European" (or PIE for short) in the case of the Indo-European languages.  However, historical linguists also argue that the gradual disappearance of shared traits between related languages will eventually progress to such a degree that their family resemblance entirely fades away, after a threshold of perhaps no more than 8,000 years.  Conversely, the family resemblance existing between the Indo-European languages is still discernible, suggesting that populations speaking different Indo-European languages have not been separated from one another for more than a few thousand years.  Even so, Europe and Southcentral Asia have been occupied continuously for tens of thousands of years, implying that the Indo-European languages now spoken in these regions could not have descended from the languages originally spoken there by the populations living their tens of thousands of years prior.  Instead, Renfrew argues, the establishment of the Indo-European-speaking communities currently occupying these regions must have involved replacement of older populations by an influx of PIE speakers within the last few thousand years.  In Renfrew's account, this PIE population, practicing an agricultural economy and driven by the explosive population growth that such an economy supports, expanded out of its original homeland (perhaps in Anatolia, perhaps ~8000 years ago) to overwhelm the much more sparsely distributed hunter-gatherer populations previously inhabiting Europe and Southcentral Asia.

As Alison Wylie has argued, a central component of Renfrew's support for his account is an appeal to its parsimony, and he has certainly succeeded on this point, quite well.  First, he has suggested that his account might take on global relevance if applied to the explanation of the geographic distribution of the world's other major language families (Occam's razor as universal quantification), dismissing alternative accounts in the process (Occam's razor as advocacy of necessary and sufficient causal relationships).  Second, he has formulated his account in such a way that it explains not only the language geography of Europe and parts of Asia but also the emergence of agricultural economies in Europe, and tentatively the geographic distribution of genetic variabilty there, as well (Occam's razor as the explanation of many effects by a single cause).  Third, by attributing these economic, linguistic, and genetic changes to a single process of population expansion and replacement, Renfrew has disfavored more eclectic causal accounts, for example involving a mixed process that includes the sharing of ideas and languages between neighboring groups in addition to population expansion and replacement (Occam's razor as suppression of causal terms; this book on contact-induced language change is an engaging read on contact-induced language change and may well be my favorite book ever).  Fourth and finally, Renfrew's account explicitly concedes that the ongoing process of population expansion may have varied in detail as it unfolded (e.g., regarding the rate of population expansion, the degree to which expanding agriculturalists outnumbered hunter-gatherers, and so on; Occam's razor as abstraction).

Yet, despite the simplifying ambition of Renfrew's account, few archaeologists have actually been impressed by it.  Wylie summarizes the numerous critiques that have accrued since the model was first advanced, these variously focusing on the empirical implausibility and the lack of "causal efficacy" (in other words, sufficiency) of Renfrew's account. In short, many archaeologists contend that his model runs slipshod over archaeological data and are quick to point out that these data necessitate an eclectic account.  The virtue of simplification in this case is far from obvious.

Other examples of Occam's razor in scientific practice come from the contentious debate over the cause(s) of the Late Quaternary megafaunal extinctions.  Between approximately 50,000 and 10,000 years ago, a number of large-bodied animal species in Eurasia, Australia, and the Americas went extinct, including mammoths and mastodons, woolly rhinos, giant marsupials, giant ground sloths, and a number of other large-bodied ungulates and predators.  For decades, paleontologists and archaeologists have debated what might have led to this series of extinctions, with climate change and human impacts (including over-predation, habitat alteration, and the introduction of deadly, inter-specifically contagious diseases or "hyper-diseases") being the two main contenders.  For some participants in the debate, causal accounts that suggest a combination of these various elements, or that the demise of some species owes to one factor while the demise of other species owes to the other, are regarded as "a relatively weak approach epistemologically; ... an admission of defeat rather than a breakthrough in understanding" (MacPhee and Marx 1997:209; Occam's razor as disfavoring multi-term causes).  It is worth mentioning that MacPhee and Marx instead endorsed the hyper-disease hypothesis, which has been widely dismissed for its implausibility and insufficiency.  Instead, at least some researchers are confident in their multi-cause stance.

Perhaps one of the most controversial accounts of the North American extinctions was Richard Firestone and coauthors' recent suggestion that one or more extraterrestrial (ET) bodies impacted the Laurentide ice sheet covering southeastern Canada during the last ice age, approximately 12,900 years ago, triggering the breaking up of the ice sheet, the climatic cooling episode known as the Younger Dryas (YD), megafaunal extinctions in the Americas (but not elsewhere), extensive biomass burning across North America, significant population depression and economic reorganization of the Paleoindians inhabiting North America, and the formation of a variety of distinctive geological deposits.  In the primary article advancing this account, the authors offer the synchroneity of these phenomena as evidence congruent with the ET impact event.

Once again, however, few have found Firestone and coauthors' argument compelling, in large part because ET impact events in general have not been convincingly linked to any of the various lines of evidence cited by them and in part because few if any of their critics are impressed by the unifying power of this account alone.  Instead, archaeologists, geologists, and paleoclimatologists have seen the article as a transparent play at grabbing attention and prestige for its authors.  In an intellectual climate already strained by limited research funding, researchers dedicated to understanding Late Quaternary extinctions are instead vexed by Firestone and coauthors' sensationalism for its threat at diverting funding away from the pursuit of explanations based on more credible premises.

Occam's baby and Occam's bathwater

Simplification is not the epistemological virtue that unificationists claim it to be, as I argued in my previous post.  It should by now be apparent that Occam's razor should do little to change our minds on this point, and many researchers have little patience for it (e.g., the quote with which I began this essay).  To begin with, any impression of solidarity that the frequent invocation of the rule may give is spurious, given the multiple disparate intellectual practices that are lumped together under this single, equivocal heading.  "The" law of parsimony, as it turns out, is an epistemological Mr. Potato Head, able to be remade into whichever visage best serves the researcher's argument.

As spurious as the rule may be as a mask, however, there is nothing obviously defective with any of the various practices that it lumps together.  Rather, each one deserves careful scrutiny on its own.  In so doing, we have no reason to expect that all will remain standing, but nor do we have reason to think that all will fall.  What we want to ask of each one is, "will this practice point me toward more realistic and accurate understandings of nature/the universe?  Why or why not?"

Biconditionality

Binding a particular cause to a particular effect together in a necessary and sufficient relationship certainly simplifies the labor of a researcher: the statement (x)(Cx ↔ Ex) means that, if he or she has encountered Ex, then he or she already knows what caused that state of x; Ex stands as a proxy for Cx, and explanatory accounts that are structured in this way are tremendously helpful in applied sciences, for example clinical diagnosis.  When knowing the cause is critical to successful policy-making, medical treatment, or similar, possession of explanatory accounts like this are time-saving (and stress-, life-, and grief-saving) devices.

Be that as it may, such accounts are incredibly hard to come by.  I don't mean that it is particularly difficult to formulate such accounts.  In the internet age, where hypochondria meets WebMD, it is all too easy to find hypochondriacs thinking "all patients will develop a fever if and only if they have the bubonic plague."  The ease of formulating such statements, however, is hardly virtuous, because establishing the empirical plausibility of necessary and sufficient relationships between cause and effect is a profoundly elusive enterprise.

The easy part, as it turns out, is establishing empirical support for statements with the following structure: (x)(Cx → Ex) ("every situation that exhibits condition C will exhibit condition E").  Causal accounts exhibiting this sort of structure are easy to demonstrate experimentally, a dime a dozen, really.  The hard part is getting the arrow to point in both directions, because on the contrary, it is much easier to make paired observations like

• (x)(C₁x → Ex) ∙ (x)(C₂x → Ex):  "every situation that exhibits condition C₁ will exhibit condition E, but every situation that exhibits condition C₂ will also exhibit condition E."

In other words, we are all too aware that many phenomena of interest may be explained by either of two (or more) equally plausible, mutually exclusive causes.  In archaeology, we refer to such unhappy circumstances as cases of 'equifinality' (a term borrowed from general systems theory), while geologists prefer the term 'polygeneity'.  Equifinality is what makes drawing straightforward equivalences like "fever = bubonic plague" so misinformed and medically disastrous, instead warranting the much more complicated (and expensive) enterprise of differential diagnosis.

The solution is a lot of research, not Ockhamian flag-waving and offhanded dismissal of alternative explanations, even if it means sacrificing explanatory (and financial) efficiency.  In differential diagnosis, this requires the prior establishment of symptom complexes or syndromes, combinations of signs and symptoms that are indicative of particular medical conditions:

• (x)(C₁x ↔ (E₁x ∙ E₂x)) ∙ (x)(C₂x ↔ (E₁x ∙ ~E₂x)):  "Every situation will exhibit conditions E₁ and E₂ if and only if it exhibits condition C₁, while every situation will exhibit condition E₁ but not E₂ if and only if it exhibits condition C₂.

The research efforts involved in establishing these relationships fall under the heading of symptomatology, whereas the application of such knowledge falls under the general heading of diagnosis, including its differential variety.  Note that the observation of a single symptom, in this case annotated E₁, cannot be explained unambiguously, even if both conditions C₁ and C₂ are sufficient to cause it.  Instead, a successful diagnosis may require further evaluations of a patient (though this should be balanced with other considerations).  As has been argued elsewhere, the invocation of Occam's razor to rule out explanations that do not make the same predictions is illicit, even if a part of their respective predictions is identical.

Archaeologists engage in a similar sort of reasoning: when confronted with situations of equifinality, when we really want to know which human activity led to the formation of an archaeological deposit, or if it was human activity at all, we need to draw on a body of knowledge that ties particular patterns of cultural debris to particular behavioral or natural processes.  We call this body of knowledge 'middle range theory' or 'formation theory,' which is built from 'actualistic research' (including experimental archaeology, ethnoarchaeology, and computer simulation).  Often, the archaeological reconstruction of  past human activities and natural processes requires us to draw on multiple lines of archaeological evidence when single lines prove to be equivocal.

Universal quantification

While biconditionality is hard to come by in scientific research but still worth pursuing, formulating explanatory accounts that assume universal quantification is an essential requirement.  Consider the alternative case of existential quantification:

• (Ǝx)(Cx ↔ Ex): "There are some situations which will exhibit condition E if and only if they exhibit condition C."

This formulation is capricious and unreliable; it leaves us wondering which situations are covered by the explanation and which ones are not.  In fact, on this point a logician would be quick to point out that the existential quantifier does not even rule out the possibility of universal quantification, but nor does it necessitate it; a universally quantified rule implies that the rule is also existentially quantified ("if all x are P, then some x are P, necessarily"), but an existentially quantified rule does not necessarily imply its universal quantification ("if we know that at least some x are P, then we cannot say for sure whether all x are P or not.").  Statements involving existential quantification are useful tools for description, but when applied to the task of explanation, such statements leave us in the dark as to why certain situations should exhibit well-specified cause-effect relationships while others may or may not.  Worse still, we might imagine a disingenuous researcher variously invoking and dismissing the applicability of an existentially quantified explanation to particular situations, conditional on self-serving motives rather than any honest concern for improving our understanding of nature.

Even worse would be the case of an unquantified rule:

• Cx ↔ Ex: "The individual situation x will exhibit condition E if and only if it exhibits condition C."

The rationale in making such statements is entirely obscure: why is Cx necessary and sufficient for Ex in this one situation but potentially not in others?  Such statements are entirely unsatisfying, and fortunately few researchers actually make such locally specific statements.

If we rule out these two alternatives for their indecisiveness and vulnerability to deceitful manipulation, we are left with universal quantification, with explanatory accounts that are meant to apply to every situation.  It also makes the identification of empirically inaccurate explanations easy: if the rule "breaks down" in light of empirical data, for example if its applicability seems to be conditional on some other condition that is not included in its specification, then it is insufficient and needs to be reformulated accordingly.

Abstraction

In evaluating the epistemological merit of abstraction, we should be aware of the fact that this practice exists in essential tension with universal quantification and biconditionality.  When the latter two practices are combined, in other words when our formulation of an explanatory account takes the form (x)(Cx ↔ Ex), we transform Ex into a decisive, diagnostic outcome of Cx, dodging the pitfall of making noncommittal statements like:

• (x)(Cx ↔ (Ex ˅ ~Ex)):  "If and only if any given situation exhibits condition C, it will either exhibit condition E or it won't"; or
• (Ǝx)(Cx ↔ Ex) ∙ (Ǝx)(Cx ↔ ~Ex):  "There are some situations that exhibit condition E if and only if they exhibit condition C, and there are some other situations that don't exhibit condition E if and only if they exhibit condition C."

However, when we deliberate insert an imprecise expression of E into the formulation (x)(Cx ↔ Ex), we sacrifice a degree of the decisiveness we originally gained by combining universal quantification and biconditionality.  In theory, we might even accomodate for such a large degree of imprecision in the formulation of E that the noncommittal statement (x)(Cx ↔ (Ex ˅ ~Ex)) is the better fit, if we are being honest.

However, our willingness to engage in abstraction need not be seen as entailing a slippery-slope descent into explanatory impotence.  In practice, this is rarely the case, because our allowance for imprecision is usually tempered by statistical constraint: "every situation that exhibits condition C will exhibit something like condition E, even if not condition E exactly, and not a condition very different from it."  Imagine an experiment in which a group of lab mice are exposed to a performance-altering substance (the 'treatment group') while a second group remains unexposed (the 'control group').  When a mouse from one of these two groups is then placed in a maze, no individual from the treatment group completes the maze more quickly than any mouse from the control group.  However, the time to completion does vary between individuals within each group.  The results of the experiment are then formalized in terms of the following two causal accounts:

• (m)(~Sm ↔ Om):  "Any mouse will complete the maze in approximately one minute if and only if they have been exposed to the performance-altering substance."
• (m)(Sm ↔ Tm):  "Any mouse will complete the maze in approximately two minutes if and only if they have been exposed to the performance-altering substance."

While this example is hypothetical, real experiments often exhibit similar distinctions between groups, with limited or no overlap in the outcome.  Such cases illustrate the fact that constrained imprecision in the expression of E does not necessarily weaken the explanatory power of an explanatory account; we still understand the world a little better when we understand that mice that are exposed to the substance in question suffer a disadvantage of time in navigating a maze relative to those who are unexposed.  At the same time, we are being honest with the influence of a given causal condition on an outcome condition when we acknowledge the imprecision that characterizes its influence on time to completion.  The realism that such statements permit, not their parsimony, is what should convince us to accept abstraction as a good practice in formulating explanatory accounts.

Diverse effects

Unlike universal quantification, biconditionality, and abstraction, the practice of subsuming explanations of multiple, qualitatively distinct phenomena under a single account has no merit.  Renfrew sought to do so by linking the spread of agriculture and linguistic and genomic geographies to a single process of population expansion and replacement.  Similarly, Firestone and coauthors sought to do so by linking American megafaunal extinctions, economic reorganization, climate change, and the formation of a handful of poorly understood geologic deposits to a single extraterrestrial impact.  But why should we be impressed by such syntheses?  On the contrary, we observe coincidences all the time in the course of our daily lives, and this ought to be reason enough not to be taken in by such grand syntheses.  Instead, the burden is on the researcher to provide a convincing argument for why qualitatively distinct phenomena ought to be linked to a common cause.

Suppression of causal terms

There is also little reason to think that the number of premises involved in a causal account should be few in number.  The question is not "how many working parts are invoked?" but rather "how plausible is the particular combination of working parts that has been invoked? (what is their joint probability?)."

My own work in archaeological demography focuses on identifying factors that influenced patterns of stability and change in the population growth rates of high-latitude hunter-gatherer populations of the past.  The population growth rate is a net balance of the 'four flows' of demography - fertility, mortality, in-migration, and out-migration - and therefore any explanation for patterns of stability or change in a population's growth rate record must refer to a change in one or more of these flows.  It would be convenient for me if I could pursue my explanatory efforts under the assumption that any observed change in my study population's growth rate was caused by a change in a single flow, but such singular changes are rare.  Whatever factors have led to change in one flow have the stubborn habit of driving change in one or more of the others, as well.  Changes in per capita subsistence productivity, for example, can influence fertility (with nutritional income bearing on reproductive health and/or decision-making), mortality (through deficiency diseases, compromised immune systems, and/or violence fueled by subsistence shortfalls), and/or migration ("stick around if food is bountiful; consider moving on to more productive lands if it is not").  Ironically, explanations for growth rate change that focus on changes in individual flows are frequently less plausible than those that focus on changes in multiple flows.

This example also illustrates another reason that most realistic (= plausible) explanations involve multiple terms.  In thinking about the factors that influence population growth, the four flows are proximate determinants: any factor other than fertility, mortality, in-, or out-migration that has an influence on population growth must act through one or more of these four flows.  Environmental change, predation, infectious disease, subsistence productivity, education, contraception, violence, genetic disorders, and other factors that might bear on population growth are thus most accurately conceived as distal determinants, and any explanatory effort focusing on such indirect influences must therefore include as many causal terms as it takes to adequately describe the chain of influences linking the indirect determinant of interest to population growth.  This, I think, is exactly the sort of necessary plurality that Ockham had in mind when he warned against unnecessary plurality.

Newton's razor

In the end, there is no reason to pay such deference to Occam's razor as unificationists do.  When it is invoked, the effect (at least for those who buy it) is to prevent a more thorough scrutiny of the plausibility and sufficiency of an explanatory account; instead, the target is a low cause-to-effect ratio, with lower ratios facilitating more redundancy in explanation.  In the process, all manner of intellectual activities are offered as examples of good Ockhamian behavior, conjuring the impression of epistemological solidarity among those who invoke it, despite the demonstrable qualitative differences standing between these practices.

Newton's razor, on the other hand, has considerable appeal to it: "we are to admit no more causes of natural things than such as are both true and sufficient to explain their appearances."  Whereas Occam's razor is primarily a numbers game, Newton's makes no particular demand for economy but instead requires sufficient and plausible causes.

On the matter of sufficiency, it is important to distinguish between formal sufficiency and causal efficacy.  From a strictly grammatical standpoint, it is easy to construct causal accounts that follow the form

• (x)(Cx → Ex)

for example "pre-menopausal women who continue to live in close proximity to each other for extended periods of time will exhibit increasingly synchronized menstrual cycles over time."  On the other hand, not all such constructions are equaling compelling.  Many researches call this often-repeated account into question for its lack of causal mechanisms.

Establishing plausibility is a separate issue.  We might conceive of causal accounts that make a lot of sense hypothetically but whose causal terms are unlikely to be true (= implausible).  For example, it does not take any great act of imagination to envision a scenario in which the terrestrial impact or air burst from a large extraterrestrial object leads to a cataclysmic extinction event.  This is the favored account for the extinction of the dinosaurs approximately 65 million years ago, and if popular entertainment is any measure of the credibility of mechanism in a causal account, the back-to-back release of Deep Impact and Armageddon in 1998 is a further indication of this scenario's general credibility.  (On the other hand, the idea of menstrual synchrony is frequently enough repeated that popularity should not be treated as the final arbiter of sufficiency).  Instead, what makes Firestone and colleagues' explanation of American megafaunal extinctions and economic and climatic change so unconvincing is that, despite centuries of geological, paleontological, and archaeological research in North America, none of the tell-tale symptoms of an ET impact at aprroximately 12,900 years ago have made themselves known.  Instead, Firestone and colleagues make their case based on a round-up of nonspecific lines of geological, paleontological, and archaeological evidence.  The medical analogue would be a clinician who diagnosis an unconscious patient with Hantavirus Pulmonary Syndrome based on the observation of a mild cough, split ends, and a swollen thumb.  Such malpractice borders on gross negligence, and one would hope that censure, if not revocation of the clinician's medical license, would follow.  Or, if you favor a less socially charged example, a healthy lawn may require watering, and lawns in rainy areas may do well on that count, but if I have a healthy lawn in a drought-stricken area, it's not because of the rain.

In short, what Newton's razor demands of any explanation, and what we should demand of it as well, is not that it is efficient but instead that it makes sense, not only in an abstract way (sufficiency) but also when it is applied to a particular case (plausibility).  If Newton's razor saves us any effort, it is only as a side-effect: in shaving off the incredible from consideration, we don't have to waste the time, or limited research funding, investigating it.

Is science all GUTs and TOEs? An anatomy lesson in science as it never was (Scientific R&D, Part 2.1.1)

Apologies to readers for my quarter-year hiatus.  Both of you.  As it turns out, actually trying to get research projects off the ground while simultaneously making a living gets in the way of writing about science, though fortunately not of thinking about it.  In the interim since my last post, I have taken a consulting position at a center that provides computing resources (and support from consultants like me) for social scientists, which is pretty cool.

To get back up to speed, previously I argued that the scientific enterprise exhibits a division of labor similar to a manufacturing industry, with separate divisions dedicated to Research and Development (R&D) and Quality Control (QC).  In this metaphor, the "products" that the R&D people develop are explanations of the phenomena that we encounter as we go about our daily affairs (although scientists in many fields now regularly encounter phenomena that we would never in a million years encounter without deliberately seeking out strange new things ... peculiar bioluminescent critters at the bottoms of the oceans; bizarre goings-on at the farthest reaches of our galaxy and of our universe; subatomic particles with outlandish names like "neutrino," "quark," and "boson"; and so on).  The people in the QC division, on the other hand, evaluate just how good these explanations actually are, whether they be freshly minted by R&D or whether they've been "on the market" for a while.  More literally, QC tests these explanations for their goodness of fit with the world they were designed to explain, by subjecting them to further observation.  Ideally, when QC discovers that a given explanation does not fit well with observation, this explanation is discontinued, and it's back to the drawing board for R&D.  Obviously, the labors of the two divisions are complementary (in an antagonistic sort of way), because the R&D people are great at brainstorming new explanations but incapable of getting rid of bad ones, while the QC people are incapable of generating new explanations but great at making room for better ones.  (As with any metaphor, this one falls apart if pushed too far.  Importantly, most researchers do not exclusively work in one division or the other; most of us spend our time bouncing back and forth between the two labors.)

I also argued that R&D's operations are not distinctively scientific; people have been in the business of coming up with ideas about how our world works for a long, long time, long before scientists achieved any sense of scientific self-awareness, and long before navel-gazers like me began to think so hard about what scientists really do or how this compares to/contrasts with what other people do.  Instead, it is the operations of the QC division that makes the scientific enterprise definitively scientific.  what is unique about the scientific production of knowledge is that it endangers ideas about the way the world works - hunches and sacred beliefs alike - by pitting them against observation.  In other words, if you aren't willing to endanger your understandings of the world in the crucible of observation, you aren't being a scientist.

While it is QC's activities that make science science, this in no way implies that we should remain indifferent to the operations of the R&D division.  On the contrary, how the R&D people conduct their business has a major influence on the quality of ideas that eventually make it into our belief systems.  Consequently, an audit of R&D's standard operation procedures is worth doing.  In my last two posts, I began to audit R&D by exploring what it is that catalyzes the division's operations in the first place.  The answer to this question is that R&D scientists begin by being puzzled about the world's peculiarities, leading them to explicitly ask questions about such things.  The understandings that R&D produces and passes along to QC are initially generated as answers to such questions.

But that is only the beginning of the life of R&D's ideas, and we are arguably more concerned with what happens to them after they are born (or put on the market, to go back to the earlier metaphor). Given that some of these ideas are going to stick around for a while if they make it through QC, what qualities do we want them to have?  In this post, I come at this question somewhat negatively, by dismantling a widely held misunderstanding about what kinds of explanations R&D scientists should be putting out there.  This misunderstanding is so widely held, in fact, that many scientists share it, particularly new ones, and some even regard it as a necessary condition for scientific knowledge production.

How should scientific knowledge be organized?

Way back in my first post, I stated that one of the goals of scientific practice is to achieve better-organized understandings of our world.  This goal has tremendous appeal if for no other reason than that good organization makes for the clear and efficient communication of scientific understandings to potential consumers.  Of greater importance (in the minds of many of science's most outspoken advocates) is the assertion that the organization of our knowledge about the world ought conform to
the order characterizing the world itself; if the world is governed by a relatively well-organized and simple set of laws or principles, then our belief systems ought to be, as well, and preferably in the same way.

This is a pretty huge and important claim, not only because of the frequency with which it is presented as one of the fundamental axioms of scientific practice, but also because it is not a salient feature of many other approaches to knowledge production.  Given the quickness with which some scientists assert the mandate of seeking better-organized beliefs, we ought to understand what we actually mean when we say 'well/better-organized.'  As it turns out, as with so many other important and commonly used words, we think we have a pretty good grasp on what 'organization' means right up until we start thinking about it.

What is worse, when we actually examine how scientists use the word, we discover that their usage conceals a few important alternative meanings, increasing the opportunity for equivocal or amphibolous arguments.  One of the most well-developed outlooks on organization in science, called "unificationism" (because no label is worth using if it has any less than seven syllables), collapses three separate meanings under this single heading, imposing all three mandates on scientific practice in a single breath.  First, there is the minimal requirement that no two understandings about how the world works can contradict each other, because the world quite simply cannot both be one way and its opposite (this is what logicians refer to as the "law of non-contradiction").  Second, there is the requirement that scientific knowledge ought to be well-integrated, meaning that that multiplicity of beliefs that populate our belief systems should be tied together as networks of belief, with a clear linkage tying any given belief to at least one other.  And third, there is the requirement that scientific knowledge ought to simplify these networks of belief, either by reducing the number of distinctive beliefs that populate them, or by imposing a specifically hierarchical structure upon the network which collapses the diversity of beliefs down as merely specific cases of increasingly general principles.  The relevance of these three dogmas for scientific practice is that they put the burden of unification on R&D scientists: if a freshly minted hunch about how the world works is to leave the drawing board for trial by QC, it should be the sort of hunch that would fit well with the preexisting array of knowledge, and preferably simplify it a bit.

Considered in isolation, each of these three requirements already makes a bold assertion about the ideal structure of scientific knowledge.  Thus, considered together, their collective boldness is too great to continue accepting them without further reflection and scrutiny.  On the contrary, we need to ask two questions of each requirement: first, is it practically achievable, and second, will it guarantee a more realistic understanding of the world if achieved?  My first contention is that well-integrated belief systems are more realistic than less-integrated ones, but these are not always practically achievable.  Even if such integration remains to be achieved, however, my second contention is that the much weaker criterion of internal consistency should be maintained at all costs.  ('Integration' and 'internal consistency,' by the way, are often indiscriminately lumped under the common label 'coherence,' so it might be useful to think of integration as a strong variety of coherence and internal consistency as a weak variety, but more on that below.)  My third contention is that the unrelenting push for simplification is not only not always feasible (for the same reason that network integration is not) but more importantly is an unwarranted rule of thumb, with the potential to yield less realistic understandings rather than more.  In short, if we as scientists are being honest with ourselves, then we need to confront the fact that the unificationist agenda is not only impracticable but also unlikely to yield the realistic understandings we desire.

Unification as integration

Scientific inquiry is undeniably oriented toward clarifying the relationships that exist between the entities that populate nature/the universe, their properties and behaviors, and variability therein.  Scientists are not satisfied with the vague intuition that everything is connected.  Instead, we want to understand the particular details about how any two things or sets of things are connected, as well as what the strength of this connection actually is.  So, it is hard to deny that integration is at the heart of scientific practice.  Almost always, the new beliefs that R&D posits are beliefs about previously unexpected linkages between entities that we want to understand better.  All else being equal, then, the addition of such understandings to a prior collection of beliefs will tend to increase its degree of integration.  There are, however, a couple of factors that work in the opposite direction.  First, there are instances of subtraction, which can occur in either of two ways: (1) previously accepted items of knowledge are challenged and ultimately dismantled by QC work; or (2) some items of knowledge are simply forgotten: their currency diminishes as they age until eventually, they succumb to their senescence and vanish out of mind.  By either route, the result is the dissolution of a previous linkage, fragmenting the network of beliefs to a degree.

Second, there is a logistically problematic dynamic, in which the relentless outward/downward/upward/inward expansion of science into new frontiers occurs at a pace that, from all indications, is outstripping R&D's finite capacity to integrate incoming items of knowledge.  On this point, it is perplexing that some of science's most well-known spokespeople are on the one hand keenly sensitive to the vastness of the unknown frontiers (there are more quotes on this topic than I have the room to recite) and on the other so insistent that we might one day hope to integrate all of the knowledge that will eventually come in about these frontiers.  As it is, our capacity to hold items of belief in memory is limited enough that no single individual can claim to possess their own personal and exhaustive copy of current scientific knowledge; the global body of knowledge about the universe (some of it scientifically sanctioned, some gained by other means), resides not in the memory of any individual but instead in an abstract, collective memory, comprising human memory as well as the various external information storage devices that we rely upon so heavily.  As one philosopher of science points out, we are obliged to take a piecewise approach to our understanding of the universe - i.e. in which one set of understandings applies to some aspects of our universe while other sets apply to other aspects - as a result of our inherent limitations.  Thus, in conjunction with the proliferation of scientific research, our intrinsic cognitive limitations make the prospects of synthesizing scientific knowledge bleak indeed, more so with each passing day.  Because of this and because of the relentless give-and-take of the R&D/QC antagonism, the notion of a perfected integration of scientific knowledge is quite simply antithetical to scientific practice, not the inevitable end of it.  (See these two articles, [1] and [2], on the state and future of particle physics in the wake of the discovery of the Higgs' boson and this one on the idea of culmination in physics more generally.)  In short, we will likely never reach a point where we can actually test the oft-cited claim that everything out there is related to everything else out there, but we can at least say, with considerably greater confidence, that our current state of knowledge is most certainly not one in which our beliefs about everything are connected to our beliefs about everything else.

Giving up on the quest for global synthesis, however, should not discourage us from seeking out more local connections.  Unlike global synthesis, small-scale integration is the stock and trade of science - we actually do it, all the time! - so it is anything but futile.  Ironically, it is also these small, self-restrained projects, that reassure us that we are not hopelessly adrift in a sea of disjointed ideas or a universe of unrelated things.  In my opinion, it is particularly exciting when we identify compelling linkages that cross-cut the conventional disciplinary boundaries.  (Though I am biased in this respect, because my two chosen disciplines - archaeology and demography - both celebrate their interdisciplinarity, more so than, say, physics.)

Similarly, learning to accept the eclecticism that inevitably characterizes our belief systems should not be mistaken for also accepting contradictions between locally networked subsets of belief, for two reasons: first, the potential to integrate presently unrelated sets of belief in the future remains open provided that they do not possess contradictory elements.  And second, we axiomatically accept that the universe itself does not possess any self-contradicting elements: if something is true of the world, it cannot also be false of it (again, this being the law of non-contradiction).

Unification as simplification

While the requirement of integration is problematic in its own right, this problem is relatively minor compared to the additional requirement that we seek to simplify our belief systems through the imposition of hierarchical structures upon them.  Given the preceding critique of global integration, we can already conclude that global simplification is all the more impracticable.  On the other hand, just as with research focused on achieving local integrations, many researchers conduct research focused on local simplifications, and sometimes these do stand up to the scrutiny of QC.

To expand a bit, what this kind of hypothesis does is reduce the number of phenomena that require unique explanation, instead accounting for multiple outcomes as if redundantly governed by the same principle.  These one-cause-to-many-effects statements are sometimes called "covering laws," while research that is conducted in their pursuit is sometimes labeled "nomothetic" (from Greek 'nomos' [custom, law] + 'theto' [to place]) or "nomological" (from Greek 'nomos' [custom, law] + 'logos' [discussion, discourse]) ... though these labels don't have as much currency now as they did a few decades ago.

Hiding under the label of "nomothetic/nomological research," however, we can distinguish between two subtly different kinds of activity: first, there are those research activities that posit and test statements that treat a particular set of phenomena as if commonly governed by a precise rule, which can then be tested as a hypothesis against observational data.  For example, I could propose that my car's average MPG for a given period of time (call it TMPG) conforms to the relationship

    TMPG = HMPG(p) + CMPG(1-p)

where p is the proportion of miles spent on highways during the study period, HMPG is the average MPG for highway driving, and CMPG is the average MPG for city street driving.  While this is a relatively low-level law pertaining to a rather trivial corner of all of the amazing things that go on in nature/the universe, it is nonetheless a law insofar as it asserts that TMPG values for different time periods conform redundantly to a single sort of relationship: every single TMPG is related to p, HMPG, and CMPG in the same sort of way as every other TMPG.  This approach is remarkably different from any other approach that would assert that TMPG values for different periods are each dictated by their own equation, involving different mathematical operators, different orders of operation, and/or different variables than p, HMPG, or CMPG.  I can scrutinize the accuracy of this lawful understanding of TMPG if I also have some prior knowledge of HMPG and CMPG for my car and if I can measure p for particular driving periods.

The second variety of nomothetic research is what I referred to in my previous post as "theory-driven inquiry": theories provide a very general, skeletal framework of a story within which the researcher might try to fit many particular phenomena.  In fact, it is their lack of detail that makes theories so flexible.  For example, modern medicine has greatly benefited from the rise of the germ theory of disease, which suggests that the failure of biofunctions in organisms is sometimes caused by the invasion of those organisms (the hosts) by other, smaller organisms (the "germs" or parasites), which then exploit the body of the host as a resource, disrupting the host's normal biofunctions in the process.  The germ theory of disease is general enough that it tolerates different sorts of germ - prions, viruses, bacteria, protazoa, fungi, arthropods - each of which exploit their hosts in different ways.  Unlike formalized laws (as in the TMPG example), theories cannot be directly tested.  Additionally, the failure of a researcher to convincingly fit a case to a theory does not indict the theory, which on the contrary may go on to make sense of lots of other phenomena.  For example, while our understanding of certain diseases fit well within the bounds of the germ theory of disease, others instead fit under toxicological, congenital, or genetic theories of disease.  Similarly, evolutionary biologists now distinguishing between four separate kinds of mechanism leading to evolutionary change - mutation, drift, gene flow, and selection - yet the fact that some cases fit better with selection and others with mutation, drift, or gene flow does nothing to undercut the credibility of any one of them.

The distinction between these two different kinds of nomothetic research is important for a number of reasons, one which will matter below, others of which I will revisit in future posts.

What makes simplification so controversial, however, is not whether we can achieve it at either a global or a local level (no and yes, respectively) but instead whether the dynamics of nature/the universe conform to such simple, hierarchically structured principles, globally or locally.  The argument goes that, if the universe itself is so governed, then so should our belief systems be.  Under this assumption, Richard Feynman even went so far as to assert that research that is not directed toward formulating and testing simplifying hypotheses is not scientific.  As an example of this sort of simplifying research, many particle physicists are on a quest in pursuit of a "grand unified theory" (GUT) which would collapse three separate forces governing how different bits of matter interact with each other as variants of a single force (the electromagnetic, strong nuclear, and weak nuclear forces, respectively).  Assuming that such a unification can ever be achieved, a "theory of everything" (TOE) would further collapse gravity and this three-in-one force into a four-in-one force.  This has not yet happened.

Physicists are hardly alone in their advocacy of the simplifying agenda; researchers in many other fields espouse it, as well.  The authors of Principles in Virology, for example, offer a quote from Nobel Prize-winning bacteriologist Al Hershey in defense of their unificationist approach to textbook-writing: "The enduring goal of scientific endeavor ... is to achieve an intelligible view of the universe.  One of the great discoveries of modern science is that this goal cannot be achieved piecemeal, certainly not by the accumulation of facts.  To understand a phenomenon is to understand a category of phenomena or it is nothing."  (The authors discuss the importance of teaching general principles further in this Microbe World podcast, beginning approximately 31 minutes in.  Al Hershey comes up at 44 minutes in.)

The most ambitious unificationists are those who insist that this simplifying operation should aspire to such grand proportions that it dissolves all disciplinary boundaries.  Overwhelmingly, it is the physicists who are posturing to subsume all other disciplines:

http://xkcd.com/435/

Not long ago, I ran across a particularly self-assured advocate of this viewpoint (a recent graduate of physics, I suspect) in an online comments thread, who asserted that

In the scheme of things physics deals with much more basic, lower abstraction level, phenomenon, that does allow for much better controlled experiments than social sciences can achieve. Hypothetically, with knowledge of physics, enough data collection along with sufficient levels of computing power, one could calculate everything, including animal and human behavior. We are very far from being able to what I just suggested but my point is that physics is the science upon which all others are built. Physics deals with the most basic forces or nature, that all other sciences must deal with at some level. ("Strato Man")

(Note the inconsistency in verb tense between his implication that physics is presently "the science upon which all others are built" on the one hand, and his future-tense assertion that such a subordination might some day be possible, though we are very far from it currently.)

As if the physicist's arrogant ambition in this matter weren't bad enough, it is made all the more insulting when it is accompanied by smug condescension regarding other disciplines' inferior ability to accomplish their own research goals.  The human/social sciences in particular bear the brunt of such condescension, for example,

Any physicist threatened by cuts in funding ought to consider a career in the social sciences, where it ought to be possible to solve the problems the social scientists are worked up about in a trice (John Gribbin, from The New Scientist, quoted by Duncan J. Watts in Everything is Obvious*).

Similarly, in Feynman's reflections on the centrality of laws in science (video linked above), he also asserts that "social science is an example of a science which is not a science," whereas he is privileged with the

advantage of having found out how hard it is to get to really know something, how careful you have to be about checking your experiments, how easy it is to make mistakes and fool yourself.  I know what it is to know something, and therefore, I can't ... I see how they get their information, and I can't believe that they know it.  They haven't done the work necessary, they haven't done the checks necessary, they haven't done the care necessary.  I have a great suspicion that they don't know this stuff.

(This attitude also reveals Feynman's failure to recognize that scientific knowledge is spectrum rather than a binary opposition, spanning all the way from untested hunches, through proofs of concept, to well-supported items of knowledge.)  The over-confident physics graduate I mentioned above echoed Feynman in labeling himself "a physicist who understands the concept of testable theories" and in asserting that slapdash research by social scientists (in this case including sociobiologists) is to blame for public distrust of science in general.  It is as if we (social scientists) are children playing dress-up in our parents' (hard scientists') clothes and accessories (smocks and goggles, I suppose).

Nor does the condescension stop there: not only are social scientists regarded as pseudoscientists for our avoidance of covering laws (not always true, by the way), then treated as dilettantes for our inability to conduct rigorous tests and checks, but our chosen subject matter is itself trivialized, for example in Feynman's dismissal of ethnobiology:

Curie is similarly disinterested in people:

And Rutherford has no interest whatsoever in anything that is not physics:

Not surprisingly, the arrogance of physicists is so pronounced that it has become an easy and frequent target for caricature, for example Sheldon Cooper's dismissal of the social sciences as "largely hokum" (The Big Bang Theory, Season 2, Episode 13: "The Friendship Algorithm"), and also this:

http://xkcd.com/793/

Critiquing simplification

Before I get into the meat of my critique, I'd like to start off by addressing a word-choice pet peeve that comes up frequently in this discussion: unificationists love to describe simple laws as 'elegant' ("pleasingly graceful and stylish in appearance or manner"), usually in lieu of 'simple' as if the two were synonymous.  To my mind, this is a really perplexing and idiosyncratic usage, given that 'sophistication' is also frequently associated with elegance.

Now, to the meat of it.  To begin with, it bears repeating that global or other far-reaching simplifications are prohibitively impractical.  Short of possessing a computer as powerful as Douglas Adams' Deep Thought, it is doubtful that we could ever "calculate everything, including animal and human behavior" as derivatives of basic principles of physics.

(image by H. Svanegaard)

Nevertheless, those committed to the simplification program employ one or more work-around strategies to make it so, though unfortunately, these are without exception fallacious.  The first of these strategies focuses on the 'explanandum' (i.e., the target of explanation, the phenomenon to be explained; plural 'explananda'), while the second focuses on the 'explanans' (i.e., the phenomenon or phenomena invoked as causes of the explanandum; plural 'explanantia').  The first strategy involves a bait-and-switch presentation of the explanandum:

• Bait: describe the collection of explananda in detail, emphasizing all of those variables about them that make them so puzzling and worthy of curiosity.
• Switch: without explicit announcing it, narrow one's explanatory focus to only a small handful, or even a single puzzling variable, about these explananda.  Attempt to explain this reduced set rather than the larger original set, without letting on that you're overlooking the rest.

This sort of reasoning commits the fallacy of redefinition.

The second strategy involves attempting to explain the explananda with reference to only one explanans.  To go back to the gas mileage example from earlier, a researcher employing this second strategy might pose TMPG as a response solely to the time spent idling the vehicle (call it i):

    TMPG = i(C)

where C refers to some constant factor by which the variable i is multiplied, their product being TMPG.  As statisticians know, and as you should know too, it is often empirically possible to assess the likelihood that proposed relationships like this one are true and, assuming that they are, what the value of constants like C are.  What makes this strategy so problematic is that it disregards the residual amount of variation that is not accounted for by the simple formulation.  If the research is being honest, they will supplement the simple formulation with an additional term describing this residual variability, e.g.

    TMPG = i(C) ±e

where ±e denotes this residual variation (or 'margin of error' or 'error term' as it is commonly called).  Furthermore, most researhers will not be satisfied to leave the explanation at that.  Error terms are thorns in the side of researchers, and only the most devout unificationist would recoil from the idea of revising this equation if it means making it more complicated, even if doing so would reduce the size of ±e.  The more appropriate response, most researchers would concede, is to continue to make revisions to the equation that do minimize ±e.  For example, in thinking about the number of miles I have driven on the highway, the number of miles I have driven on city streets, and the amount of time I have spent idling, I might suggest the following:

    TMPG = TM / [TM(p)/HMPG + TM(1-p)/CMPG + i(C)] ±e

where TM is the total number of miles driven over a given time period and all other variables are as above.  Nor is this revised law exhaustive or final; in the future, I might add in additional terms for tire pressure, which is in turn influenced by ambient temperature, and further note that HMPG and CMPG will vary between automobile models or even between individual vehicles.

This second strategy is founded on the notion that simpler = more realistic, in which case we might indeed regard it as an epistemological virtue.  Yet, as trivial as the law of gas mileage may be, it brings us face-to-face with a contrary reality: the pursuit of realism in our understandings comes at the expense of simplicity, not part and parcel with it.  If this is so, then this second strategy instead falls afoul of the fallacy of reductionism (also known as 'the reductive fallacy' or the 'single cause fallacy').  Of course, some degree of simplification is a necessary trapping of research, and researchers often choose to start the research cycles of their careers by testing simple hunches, fully expecting that these are not going to pan out.  But what makes unificationist simplification so problematic is its insistence that what looks to most like a partial explanation is a complete one, or at least one that has been unburdened by the inclusion of unimportant minor details.  David Hackett Fischer describes this fallacy in the context of historiography:

The reductive fallacy reduces complexity to simplicity, or diversity to uniformity, in causal explanations.  It exists in several common forms, none of which can be entirely avoided in any historical interpretation.  As long as historians tell selected truths, their causal models must be reductive in some degree.  But some causal models are more reductive than others.  When a causal model is reductive in such a degree, or in such a way, that the resultant distortion is dysfunctional to the resolution of the causal problem at hand, then the reductive fallacy is committed.  (Historians' Fallacies)

Many of the tentative GUTs and TOEs that have been conceived to date run afoul of this fallacy, which probably accounts for why there are no successful GUTs or TOEs yet, at least in part.  Physicists would do well to heed the cautionary tale that an uncompromising push toward simplicity will result in simplistic rather than realistic understandings, commonly attributed to Einstein (one of their own).

It is also worth noting that, even if a given explanandum can be reduced to a constant law as simple as something like "TMPG = i(C)", this explanation still leaves unexplained the variability in i driving the variability in TMPG.  Unificationists often make the mistake of thinking that the algebraic specificity of the law and the constancy of the constants it invokes together constitute a complete explanation, when in fact the variability of its variables is also an integral part of the explanation.  "Complete explanations" are mythical and necessarily elusive because any complete explanation is one in which variability in the causal variables is also explained.

Opposite the simplification agenda is the 'emergence' perspective, which argues that the properties exhibited by macroscopic entities or processes cannot be wholly reduced as the mere sum of their microscopic parts.  (Here, I use the terms 'macro-' and 'microscopic' not to refer to things that can be seen with the naked eye versus with the aid of a microscope, but instead to entities or phenomena existing at different scales: elementary particles to atoms, atoms to molecules, molecules to compound units of matter, ..., individual organisms to societies, and up and up and up.)  At best, the variables that account for higher-order entities or phenomena may include attributes about the microscopic things that purportedly constitute them, but this is rarely enough to wrap up a compelling account.

It should also be noted that there is one faction in the emergence community, sometimes going under the label 'weak emergence,' that is in fact nothing more than a clandestine unificationist attempt to reign emergence back in, working from the inside to bend it back to the same old agenda.  The change of label, however, does absolutely nothing to undo the multiple criticisms that unificationism suffers.

So, the simplification program is conceptually bankrupt, and not surprisingly, the arrogance of those who have long advocated it (I am looking at you, outspoken physicists) has proven premature:

I think I can say that the problems sociologists, economists, and other social scientists are "worked up about" are not going to be solved in a trice, by me or even by a legion of physicists.  I say this because since the late 1990s many hundreds, if not thousands of physicists, computer scientists, mathematicians, and other "hard" scientists have taken an increasing interest in questions that have traditionally been the province of the social sciences - questions about the structure of social networks, the dynamics of group formation, the spread of information and influence, or the evolution of cities and markets.  Whole fields have arisen over the past decade with ambitious names like 'network science' and 'econophysics.'  Datasets of immense proportions have been analyzed, countless new theoretical models have been proposed, and thousands of papers have been published, many of them in the world's leading science journals ....  Entire new funding programs have come into existence to support these new research directions.  Conferences on topics such as "computational social science" increasingly provide forums for scientists to interact across old disciplinary boundaries.  And yes, many new jobs have appeared that offer young physicists the chance to explore problems that once would have been deemed beneath them.

The sum total of this activity has far exceeded the level of effort that Gribbin's offhand remark implied was required.  So what have we learned about those problems that social scientists were so worked up about back in 1998?  What do we really know about the nature of deviant behavior or the origins of social practices or the forces that shift cultural norms ... that we didn't know then?  What new solutions has this new science provided to real-world problems, like helping relief agencies respond more effectively to humanitarian disasters in places like Haiti or New Orleans, or helping law enforcement agencies stop terrorist attacks, or helping financial regulatory agencies police Wall Street and reduce systemic risk?  And for all the thousands of papers that have been published by physicists in the past decade, how much closer are we to answering the really big questions of social science, like the economic development of nations, the globalization of the economy, or the relationship between immigration, inequality, and intolerance?  Pick up  the newspaper and judge for yourself, but I would say not much. (Duncan J. Watts, Everything is Obvious*)

It is also refreshing, though no less misguided, to see the unificationist agenda aimed against physics

("The Big Bang Theory", Season 4, Episode 3)

In the end, the main virtue of simplifying research is the ease with which its products can be transmitted both among fellow researchers and between the scientific community and the general public.  Simplification undeniably leads to the production of easily packaged, short communications, hence its practical appeal.  Nevertheless, in light of the preceding critique, we do have to ask, "is it better to effectively communicate a message that is inaccurate in its denial of its incompleteness, or to suffer the burden of trying to communicate complicated but accurate - though still incomplete - messages?"  In approaching simplification as an empowering enterprise, we have to wonder whether it is the kind of power that we would actually want to wield.

Exploiting disunities

Disunity, as it turns out, is empowering in its own right.  As I have previously mentioned, QC approaches its scrutinizing labor in an open-ended manner, periodically revisiting accepted and well-supported beliefs from new angles, usually by bringing new lines of evidence to bear on the review.  QC's philosophy in doing so is this: if new lines of evidence eventually topple a long-standing hypothesis in a way that previous evidence could not, then we are not only successful in ridding ourselves of a bad idea but also in identifying a shortfall of that previous evidence.  On the flip side of the coin, when multiple lines of evidence appear consistent with an accepted understanding, this mounting evidence reinforces the strength of the belief - a "miracle argument" or "argument by convergence" as it sometimes called.  Here is the problem: well-integrated networks of belief can often though unexpectedly work against our ability to accomplish such multi-line testing.

For arguments by convergence to be valid, it is absolutely necessary that each new line of evidence is independent of those employed previously.  If they are not independent - if the new line of evidence is correlated with older lines of evidence - then it is unlikely that the new evidence will yield results that run counter to the older evidence.  The sense of renewed endangerment and of mounting evidential support that result from the use of such evidence are both illusory.  The worst violations of the criterion of independence are those in which separate mathematical summaries of a single body of evidence are offered as if novel, when in fact they are simple mathematical transformations of each other.  For example, if we were to present the frequency of successes observed in some experiment as a proportion of successes out of all trials, then re-present the same evidence as a ratio of successes to failures, we are saying nothing new at all; a proportion and a ratio on a single run of trials will tell exactly the same tale, using slightly different terms.  Fortunately, this latter kind of behavior is rare in the sciences, a rookie mistake rather than a deliberately deceitful act, largely because the oversight of more experienced scientists and peers keeps us honest.  However, it is far easier to unwittingly present interdependent lines of evidence as if independent.

This is where well-integrated networks of belief may sometimes become a liability.  In many cases, the logical connections that tie well-integrated networks together operate to increase the degree of interdependence between the lines of evidence that we might otherwise have employed.  Conversely, where two or more locally integrated clusters of belief are minimally integrated with one another, opportunities for independent lines of evidence abound provided that they both bear on the phenomenon we are interested in explaining.  Disunity is a boon for QC.

For example, in my own field of research - archaeological demography - one of the things we frequently try to do is estimate the growth rate dynamics of past human populations.  In this undertaking, we have an opportunity to double-check our estimates by studying both the age-at-death distributions of human skeletal populations and the changing frequency of archaeological sites that past populations have left behind them over time.  The first line of evidence draws upon the biology of human fertility and mortality as well as of skeletal aging, whereas the second draws on anthropological understandings of human land use and waste disposal practices, as well as the geology of landscape formation processes.

These two lines of evidence are admittedly not entirely unconnected, though the connections between them are loose and indirect.  For example, both datasets in question need to be anchored to a common timeline, and in doing so, we often (usually) use identical dating methods for both.  Most of archaeology's most well-known and widely used dating methods draw on knowledge of nuclear physics, environmental chemistry, and biochemistry.  (We do get along with physicists, I promise.)  Even so, the connection that these dating efforts introduce into our two-lines approach is incidental, not the sort that undermines the effective independence of the two lines of evidence, because our ability to estimate the ages at death of skeletal remains and to infer population growth rate estimates from these is not dependent on the timestamps we put on them.  (Amusingly, however, our ability to count the changing frequency of archaeological sites over time is dependent on these timestamps, so if our dating methods are flawed, then our two lines of evidence will actually tell conflicting stories, one of them false.)

(Alison Wylie, a philosopher of archaeology, has much more to say about disunity and its usefulness in her various works. Anyone interested in the matter should pick up a copy of her collection of essays, Thinking from Things.)

The essential tension: the life of science after global unification

Scientists are unarguably engaged in an enterprise intent on identifying linkages between different aspects of nature/the universe (but also of ridding ourselves of believing in linkages that do not exist).  These connections make for interesting opportunities to communicate with the public, particularly when they are of a simplifying sort.  Nevertheless, the unificationist hypothesis of global integration and especially of global simplification seems less likely to succeed now than ever.  First, there is a steep logistical challenge: science is growing and pushing out into new frontiers at a fast and accelerating pace, vastly outpacing the ability of researchers to accomplish the sorts of sweeping integration and simplification that unificationists envision.  Second, while the unificationist program heavily implies a culminating moment of research, in which all the pieces will finally fall into place under the coverage of a grand and "elegantly simple" law of everything, in practice the give-and-take between science's R&D and QC divisions on the contrary entails an endless process of turnover in our beliefs.  (On this count, one might even argue against Feynman that the pursuit of grand unifying laws, not the rejection of law-oriented research, is pseudoscientific.)  Third, the unificationist agenda supposes that the fabric of nature/the universe is woven out of a single thread, following a simple stitch throughout, whereas it may on the contrary be a tapestry of high thread count, woven together with a sophisticated stitch and/or many different kinds of stitch.  Realistic belief systems may therefore favor sophistication rather than simplicity, and what unificationists say we do is not matched with what we have actually done, can do, or ought to do.

The burden of these multiple criticisms suggests that the scientific community is overdue in reevaluating our relationship with the organization of belief systems.  We have seen it as a straightforward and unproblematic operation, and it is not.  It is a relationship that is tense in its very core: on the one hand, scientific R&D does generate new connections between ideas where these had not previously existed, usually at a local scale, while on the other hand the rapid expansion of science, in conjunction with the subtractive effects of QC and of forgetfulness, imposes a sort of entropy on belief system organization.  Nor, it seems, is this tension a perfect counterbalance.  If anything, the state of disarray of scientific knowledge is increasing daily.

What makes this antagonism so vexing, I think, is that not everyone is well-equipped to handle antagonistic realities.  All too often, when we are confronted with dilemmas, we err on the side of one out of the competing goals at the expense of the other, rather than seeking any sort of optimal balance between them.  Yet, it is possible - at least, I hope that it is possible - to learn to be at peace with essential tensions like this one.  On the one hand, we may fret at the vanished hope of any grand unification of belief (particularly those of us who are fond of asserting that everything is connected with everything else), but on the other hand, we may celebrate the gain in realism that seemingly comes from accepting the irreducible complexities of reality.  We may mourn the loss of efficient communication that comes with the presentation of simple understandings, but on the other hand we may embrace disunity as it empowers the ongoing work of QC.  Living with the essential tension means accepting these mixed feelings, and as undesirable as this may be, it is far better than continuing to live under the self-soothing illusion that the unificationist program once afforded.