by Mark Owen Webb and Suzanne Clark
Department of Philosophy
Texas Tech University
The Hueyatlaco Dilemma
Beds containing human
artifacts at Valsequillo, Mexico, have been dated at
approximately 250,000 years before the present by
fission-track dating of volcanic material and uranium
dating of a camel pelvis. The dilemma posed by such
dates is clearly stated in the following quotation from
the conclusions of the subject article.
"The evidence outlined
here consistently indicates that the Hueyatlaco
site is about 250,000 yr old. We who have worked on
geological aspects of the Valsequillo area are
painfully aware that so great an age poses an
archeological dilemma. If the geological dating is
correct, sophisticated stone tools were used at
Valsequillo long before analogous tools are though
to have been developed in Europe and Asia. Thus, our
colleague, Cynthia Irwin-Williams, has criticized
the dating methods we have used, and she wishes us
to emphasize that an age of 250,000 yr is
(Steen-McIntyre, Virginia, et al; "Geologic Evidence
for Age of Deposits at Hueyatlaco Archeological
Site, Valsequillo, Mexico," Quaternary Research,
The above impasse is
reminiscent of Lord Kelvin's insistence that the earth
is only about 100,000 years old based upon his
calculations of the sun's energy-producing capabilities.
Geologists thought otherwise, requiring roughly a
billion years for nature to sculpt the earth they saw.
Kelvin didn't reckon on nuclear energy, and the
geologists had the last laugh!
From Science Frontiers #21, MAY-JUN 1982. © 1982-2000
William R. Corliss
Since the publication of Thomas Kuhn’s
The Structure of
Scientific Revolutions (1970), a great many people in the
sciences and elsewhere have used
his distinction between paradigms in normal science and anomalies
both in normal science and in scientific revolutions to explain
developments in contemporary science. Not all appeals to Kuhn have
been equally illuminating.
It has sometimes seemed that those on
the fringes of established science cry “paradigm bias” to explain
why their work doesn’t get any attention when it is in fact the work
itself that is to blame. Presumably, some evidence that conflicts
with received views is ignored for good reason, and some without
good reason. When an apparent anomaly is dismissed for no good
reason, then the scientists in question are behaving badly.
they behaving “unscientifically”?
In this study, we examine in detail a particular case of anomalous
evidence meeting received view. In this case, the received view is a
theory about human origins in the Americas, and the anomaly is a
site in Mexico, the age of which is apparently in conflict with that
received theory. Without trying to decide whether the received view
is correct, or whether the anomalous evidence is worth considering
(which is, after all, a job for specialists), we will follow the
story of what happened to the scientists involved, and draw
conclusions about what can and cannot be expected from science as a
real human institution.
In particular, we will argue that, in
periods of instability in science (“revolution,” if you like), it is
in the very nature of science to treat anomalous evidence with
hostility and suspicion, even when there is little evidential reason
to suspect it.
The received view, accepted by a majority of anthropologists and
archaeologists, is that humanity did not evolve independently in the
Americas, and so must have migrated there from elsewhere. For
various genetic reasons, it seems that all aboriginal Americans are
more closely related to one another than they are to any other
populations, and are more closely related to the peoples of Asia
than those of other parts of the world. The reasonable conclusion to
draw from this evidence is that the first Americans migrated from
Asia, either across the Bering Strait or across a land bridge.
Large-scale migration by boat is unlikely, even across so narrow a
body of water as the Bering Strait, so a hypothesized Bering Land
Bridge is the best hypothesis for a migratory route.
This sequence of deductions entails a limited number of
opportunities for migration. A land route was fully available only
when there was sufficient glaciation for sea level to drop by about
a hundred and fifty feet; such a drop in sea-level is necessary for
the Bering Land Bridge (or, perhaps more properly, the land mass now
called Beringia) to appear. On the other hand, if there was so much
glaciation that land routes across North America were impassable, no
migration could take place. These two constraints severely limit the
number of opportunities for migration to special periods during ice
The best candidate for a time for that migration is generally taken
to be a period during the Late Pleistocene, about twelve thousand
years ago. Although claims of earlier migrations are occasionally
pressed on the strength of archaeological finds, the view that
humans arrived relatively recently seems to be fairly
So confidently was this view held that in 1962,
writing for Scientific American, William Haag could say,
“Man’s occupation of the New World
may date back several tens of thousands of years, but no one
rationally argues that he has been here for even 100,000 years.”
There is an impressive array of evidence
for the recent-migration view, and comparatively little for any
earlier human presence in the Americas. What seemed to be evidence
of earlier occupation has usually turned out to be misleading.
Meltzer (1993) describes the situation this way:
By the early 1950’s there were
already indications of a much earlier human presence in America.
Those hints would become broader as the years went by, until
today scores of purportedly ancient sites have appeared, some
with estimated ages upwards of 200,000 years. Each new candidate
for great antiquity brings with it fresh claims, but the outcome
remains the same. Skeptics ask hard questions. Debate ensues.
The claim is accepted by some, rejected by others, while the
rest wait and see. So far at least, the Clovis barrier remains
intact. A pre-11,500 B.P. human presence in America does not now
There are at least three impressive
kinds of evidence for a Late Pleistocene migration (or set of
evidence from Native American languages
evidence from dentochronology
evidence from mitochondrial
All three kinds of evidence point to three waves of migration, the
earliest in the Late Pleistocene, as hypothesized. The earliest
clearly datable sites so far are those at Clovis and Folsom, and
they are no earlier than 11,500 BP.
Add to these pieces of evidence the absence of clear evidence for
anything earlier, and you have a powerful argument for the
recent-migration view, which gives strong reason to be skeptical of
finds that purport to be older. Consider the kinds of evidence in
Native American Linguistics
The hundreds of thousands of languages that have been spoken on the
American continents form a bewildering variety, but many linguists
now think that they fall into three families:
The Amerind languages show the most variety, and are
geographically the most widespread, being spoken in areas from
Canada to Tierra del Fuego. These two facts argue for the relative
antiquity of the common language from which they all derive.
The Eskimo-Aleut languages are fewer in number and more similar to one
another. They are also spoken in a smaller area,
around the northern coastal regions.
The Na-Dene group is
intermediate in variety and extent. Those languages also are spoken
in areas to the south of the greatest southern extent of the
Eskimo-Aleut languages, but not so far south as the Amerind
languages. Moreover, the language groups can be arranged in order of
similarity to Old World languages, with Eskimo-Aleut being most
like, and Amerind least like, the languages spoken in Asia.
This arrangement of languages points to
three separate waves of migration, with the ancestors of Amerind
speakers arriving first. However, this relative ranking gives us
little in the way of absolute dating for the migrations.2
In the 1920’s Hrdlicka noted a trait that all Native American teeth
possess, which is also characteristic of the teeth of the people of
Northern Asia. On the basis of this characteristic, a particular
shovel-like shape to the incisors called sinodonty, he concluded
that Native Americans divided into three genetically distinct
groups: Eskimos, Athabaskans, and South Americans.
Christy Turner (1986) made a statistical
analysis of American teeth to check this classification. Looking at
other, similarly heritable characteristics of teeth, and cataloging
similarities and differences from nine thousand different
prehistoric Americans, he also concluded that Native Americans
divided into three genetically distinct groups, but he identified
the three groups more directly with Greenberg’s three linguistic
In addition to supporting the three-migrations view, the dental
evidence can give us an absolute chronology. The dental
characteristics that are identified in Turner’s study are
genetically determined, environment having little or no impact.
In this way, the evidence provided by teeth, like that provided by
blood groups, can give us a clear picture of the genetic relations
among populations. Since mutations occur in a regular way, we can
also tell how long ago two populations diverged by how many genes
they share and in how many they differ. When a gene expressed itself
in a visible and easily-preserved part of an animal, such as a
tooth, then we can use the variations in that part to date the
genetic history of the animal. In the case of humans in North
America, we can tell by distributions of kinds of sinodonty that the
North American population split from the North Asian population
about twelve thousand years ago — which confirms the
late-Pleistocene migration view.
The mtDNA Clock
Similarities in gross anatomical characteristics, and even to some
extent in the genetic code underlying them, can sometimes arise due
to similar environmental pressures, even when the two populations
are not closely related. There are parts of the genetic code,
however, that do not get expressed at all, or are expressed only in
neutral characteristics. In those genes, the regular rate of
mutation is not affected by environmental pressures. In particular,
mitochondrial DNA (mtDNA) is not subjected to the mixing forces of
fertilization, as all a creature’s mtDNA comes from its mother.
So given a reasonable estimate of how
quickly and how regularly mutations occur in mitochondrial DNA, we
can fairly accurately date when populations diverged. By that
measure, Americans split from North Asians about 20,000 years ago.
This is earlier than the other methods gave us for a first
migration, but may be accounted for by the estimate of the rate of
The Response to Anomalies
Given this impressive array of evidence, it seems eminently
reasonable to think of the Late Pleistocene migration as
established. Even though there are occasional finds that seem to be
datable to much earlier, it is more reasonable to think there must
be something wrong with the dates for those sites than to accept
them at the cost of overturning so well-grounded a theory.
The inability to explain why a site
seems to be earlier than the late Pleistocene is no bar to accepting
the late migration theory, especially if the alternative is
accepting an earlier migration while being unable to explain the
linguistic, dental, and genetic evidence.
Meltzer (1993, p. 21) characterizes the
archaeologist’s position this way:
[T]his problem is compounded by too
many false alarms. Scores of sites have been advertised as
possessing great antiquity. But on closer inspection, each has
failed to live up to its advance billing. Caveat Emptor.
Archaeologists have long memories — it’s part of our business,
after all — so it is hardly surprising that under such
circumstances any and all new claims for great antiquity in the
Americas are met with skepticism bordering on cynicism. The
response may not be commendable, but it is understandable.
Most of the archaeologists who give this
understandable response are considerably less conciliatory than
Meltzer. In fact, Haag’s response cited earlier, which dismisses
claims of extreme antiquity for human presence in the Americas as
irrational, is the norm rather than the exception. The oldest sites
that have stood up to careful scrutiny, and whose evidence is
completely unambiguous, are Clovis and Folsom, both datable to after
12,000 BCE, and so completely consistent with the Late Pleistocene
Occasionally an archaeological find seems to challenge this received
view. The specific archaeological project that is central to this
work was located at Hueyatlaco, Valsequillo, which is a few
kilometers south of Puebla, Mexico. The area had become very well
known among archaeologists due to the varied extinct animal forms.
The initial excavation began in 1962. During the continued process
of excavation five sites were discovered and stratigraphic sections
sequenced (Irwin-Williams 1967a).
The final excavation at Hueyatlaco was
concluded in 1973. Field work continued throughout the excavational
process by the members of the team, including Dr. Cynthia
Irwin-Williams and Dr. Virginia Steen-McIntyre.3
Later consultants affiliated with the project were Ronald Fryxell,
B. J. Szabo, and C. W. Naeser in continued efforts to resolve the
dating controversy surrounding the evidence accumulated during the
excavation process at Valsequillo, Mexico (Malde and Steen-McIntyre
1981). There were no irregularities in the team’s methods, and the
site was guarded to prevent tampering or accidental destruction of
evidence (Irwin-Williams 1967a).
The principal investigator on this project, Cynthia Irwin-Williams
(1978), characterized the archaeological site as an area that
contained a “kill-site” and activities indicative of butchering and
camping activities of “Early Man.”
The artifacts discovered clearly establish that they are of nonlocal
origin, ranging from a crude unifacial percussion-flaked lanceolate
object (projectile point) manufactured by a less sophisticated
group, to bifacial cutting tools, scrapers, and cutting edges,
well-made tools of an advanced nature. In her article published in
1978, Irwin-Williams states that the abundance of now-extinct fauna
in the Valsequillo area attracted early hunters. There were
locations in the area suitable for camping, and nearby were sites
suitable for slaughtering activities and sites that were appropriate
for butchering procedures because of the close proximity of small
streams. Irwin-Williams acknowledges that modern estimates regarding
the presence of man in this locale ranges from 11,000 years to more
than 30,000 years.
Controversy began in 1967, before the digs were completed. Despite
the thorough efforts and the competence of the archaeological team
members at Hueyatlaco, Jose L. Lorenzo, Director of Prehistory at
the Instituto Nacional de Antropologia e Historia, launched several
allegations regarding the integrity of the project at Hueyatlaco, El
Horno, and Tecacaxco (commonly referred to as Valsequillo). The most
significant allegation was directed to the authenticity of the
artifacts retrieved from the Hueyatlaco site.
Lorenzo (1967) alleged that some of the
artifacts had been planted by laborers working at the site and then
commingled with other artifacts in a way that made it impossible to
separate and identify the planted artifacts. The intentional
commingling of evidence, if it occurred, would raise substantial
doubts about the age of the site, as well as the integrity of the
principal investigator and other members of the archaeological team.
The allegations were addressed by
Cynthia Irwin-Williams (1967b) in the Paleo-Indian Institute
Miscellaneous Publications stating that the “allegations are utterly
without basis in truth” and that Lorenzo was motivated “by distorted
personal animosity and irrational inability to change an opinion.”
During 1969, Cynthia Irwin-Williams further refuted Lorenzo’s
allegations with written statements from three reputable
professionals in the field of anthropology and archaeology
By June of 1969, Barney J. Szabo and Harold E. Malde had completed
their attempts to date artifacts retrieved from Valsequillo, and
joined by Cynthia Irwin-Williams, published the results (Szabo,
Malde, and Irwin-Williams 1969). One important means of dating the
stone tools recovered at Valsequillo was to date the strata in which
they were found by dating fossils and other animal remains from the
Radiocarbon dating on molluscan fossils
(shellfish) which showed an age greater than 35,000 years. The
uranium method gave a result of 260,000 ± 60,000 years. A mastodon
tooth retrieved from El Horno was dated using the uranium method and
was calculated to be older than 280,000 years. Likewise, a camel
pelvis recovered from the Hueyatlaco site was dated using the
uranium method closed system at greater than 180,000 years, and
using the open system as 245,000 ± 40,000.
A horse metapodial recovered from the
Atepitzingo site in the Valsequillo area was dated using the uranium
method open system date at 260,000 ± 60,000 years. In the concluding
remarks of the article (Szabo, Malde, and Irwin-Williams 1969, p.
243) the authors noted, rather mildly, that some of these were
perhaps too old stating that,
“we cannot explain why some of
these dates are much older than expected from archaeological
In the same article, Malde commented
that one of the difficulties in evaluating the samples was possibly
due to a lack of stratigraphic markers from the field for
correlation with the various sample localities. Later (the results
were published in 1981), he and Virginia Steen-McIntyre would
collect samples of the stratigraphic layers including samples of
pumice and ash to resolve just this point.4
Additional stratigraphic information would help determine whether
the artifacts were located in an erosional trough such as a stream
channel, which would indicate that the beds bearing artifacts were
of a younger age.
This possibility raised doubts that
could not be ignored. Drs. Steen-McIntyre, Malde, and
a specialist in mapping sediment layers at archaeological sites,
returned to Hueyatlaco for the additional excavation. The work to
determine the stratigraphic sequence was undertaken in 1973. This
final excavation established a sequence of age for the first time,
showing that the artifacts did not lie within a stream channel and
thus, were not younger than the ash deposits that covered them.
With a more complete stratigraphic picture of the site developed by
the 1973 trench, it now became apparent that Dr. Steen-McIntyre
faced the problem of matching the ash and pumice deposits with a
known volcanic source for purposes of dating. More samples were
taken and examined, but none of them proved helpful in source
identification. Pumiceous glass (volcanic ash blown into the air on
eruption) contains glass shards which contain a large number of
bubble cavities, known as vesicles.
As the volcanic glass weathers, moisture
moves through the exposed surfaces. In temperate climates this
process may be completed in 20,000 years. As the pumiceous glass
becomes hydrated, the vesicles also begin to collect water. The
total filling of the vesicles may require ten million years or so.
Thus, evaluating the fill within the vesicles assists in age
Using a petrographic microscope and special light-masking
techniques, Dr. Steen-McIntyre began the task of examining the
samples of the volcanic ash layers from Hueyatlaco containing
volcanic glass and mineral phenocrysts. Phenocrysts are mineral
crystals that were growing within the liquid magma at the time of
eruption. The examination process requires approximately eight hours
of microscope time for each sample. During the microscopic
examination of the phenocrysts, Dr. Steen- McIntyre detected a
phenomenon she described as resembling a picket fence. The samples,
instead of having fresh-looking crystal surfaces, looked rather
shaggy, having a “picket fence” appearance. The volcanic glass
fragments were also weathered and had absorbed water from the soil
in which they lay until excavated.
Some of the vesicles had puddles of water in them, indicating they
were of considerable age. In previous research, Dr. Steen-McIntyre
had performed dating procedures on ash layers at Yellowstone
National Park (Steen McIntyre 1980). The samples from Hueyatlaco
bore a striking resemblance to those from Yellowstone dated at
Some zircon crystals from two of the volcanic layers, the Hueyatlaco
Ash and the Tetela Brown Mud, were given by Dr. Steen-McIntyre to
another geochemist, C. W. Naeser, to process for dating. Naeser used
the zircon fission-track dating method, which relies on radioactive
properties of certain elements. The results from this process
demonstrated the Tetela Brown Mud to be 600,000 ± 340,000 years BP,
and the Hueyatlaco ash was determined to be 370,000 ± 200,000 years
BP. The minimum age ranged from 170,000 years to 260,000 years BP
(Steen-McIntyre, personal communication with Suzanne Clark).
Szabo’s results, using the
uranium-series method, ranged in age from 180,000 to 260,000 years
BP. Naeser’s zircon fission-track method showed ages ranging from
170,000 years to 260,000 years BP. Both sets of dates agreed with
Dr. Steen-McIntyre’s observations of 251,000 years. Three separate
methods, calculated by three separate geologists, yielded similar
results, yet the results met with skepticism and hostility.
As members of the team began to complete their respective dating
methods and the results were presented to her, Irwin-Williams became
critical of the results and indicated her dissatisfaction in all of
the publications regarding the Valsequillo project by various team
members. Irwin-Williams was clearly distressed that date estimates
place human presence at Valsequillo long before 30,000 BP, the
earliest date she could accept.
It is not improbable that Irwin-Williams
feared her career was in jeopardy in light of such dates. She
certainly feared (or at least was wary of) what might happen if she
was associated with fringe elements. When, at a meeting of the
Geological Society of America, Malde and Fryxell announced their
early dates for the Valsequillo site — which dates were established
by three independent dating methods — the announcement was reported
on the UPI wire for November 14, 1973. Irwin-Williams reacted with
In a letter dated 3 November 1974 to Alan L. Bryan, a
colleague in Alberta, she said:
My capsule comment on the situation (expletives deleted) is that
this is one of the most irresponsible public announcements with
which it has ever been my misfortune to become involved. Of the
three dating methods used by Malde on the materials, two are so new
that we have essentially no information on their validity. The third
(fission-track dating) gave an anomalous result of about 300,000 ±
300,000 (in other words, no date at all).
This sounds eminently reasonable. If two of the dating methods are
experimental, and one gives an essentially worthless result, then
the dates are surely suspect. Compare the charge of irresponsibility
with the text of their announcement, as reported in Quaternary
Research (Steen-McIntyre, Fryxell, and Malde 1981):
The evidence outlined here
consistently indicates that the Hueyatlaco site is about
250,000 yr. old. We who have worked on geological aspects of
the Valsequillo area are painfully aware that so great an age
poses an archeological dilemma (Szabo et. al., 1969)....
In our view, the results reported here
widen the window of time in which serious investigation of the age
of Man in the New World would be warranted. We continue to cast a
critical eye on all the data, including our own.
This statement seems eminently cautious. Moreover, the UPI reports
that Fryxell said, at the same meeting,
“It’s not fashionable to come into a
meeting and say ‘I don’t know,’ but that’s essentially where we
are right now.”
This declaration of ignorance hardly
sounds rash and irresponsible. Moreover, Irwin-Williams seems to be
getting the fission track date wrong. Steen-McIntyre, in a letter to
J.L. Bada, cites the date given by that method as 370,000 ± 200,000;
a wide range of error, but hardly meaningless. The experimental
methods (Tephrahydration and Uranium series) have since been found
to be reasonably reliable.
Dr. Steen-McIntyre was a graduate student at the time the Valsequillo project began. She was working on her Ph.D. at the
University of Idaho and the Valsequillo project was to be her
research project. It became clear to her after three years of hard
work, that the subject of her dissertation would have to be changed
due to the controversial nature of the Valsequillo findings
regarding the age of the site as published by Szabo and Malde in
Eventually, Steen-McIntyre was
forced to choose a less controversial dissertation subject, how to
examine volcanic ash samples. Steen-McIntyre finally obtained her
degree in 1977. Between 1969 and 1973, frictions within the
Valsequillo archeological team with regard to the date of the site
were building. Malde was enthusiastically promoting an early date
(ca. 200,000 years BP), while Irwin-Williams was promoting a more
conservative, but still controversially early, date (ca. 20,000
Steen-McIntyre’s allegiance was with
Malde, but her subordinate position on the team and in the
profession of archeology led her to be more cautious. Her caution,
along with her thorough scholarship, made it possible for her to
continue to find employment. In early 1973, Virginia Steen-McIntyre
had achieved international recognition from several organizations,
including the National Academy of Science, from whom she also
received funding for foreign meetings and speaking engagements. She
worked part-time in her area of expertise for a government
laboratory, and even became an adjunct professor of Archaeology at
Colorado State University.
Correspondence between Irwin-Williams and Steen-McIntyre during the
late 1970’s shows that both were becoming increasingly frustrated
with the impasse. The Valsequillo material, mostly hard artifacts,
points to an early date, but the mass of other evidence, much of it
inferential in nature, points to a much later date. After the dating
process of the Valsequillo project reached completion and she had
obtained her degree, Dr. Steen-McIntyre attempted to publish her
article on the Valsequillo site.
She encountered serious difficulties in that regard. Delays were
often explained by excuses such as: “the article has been misplaced
or lost;” she finally managed to get her article on Valsequillo
published in November, 1981. Soon thereafter, Dr. Steen-McIntyre met
with scorn and ridicule from her peers and was once even accused of
ruining Cynthia Irwin-Williams’s career (Steen-McIntyre, personal
communication with Suzanne Clark).
Barney Szabo encountered similar difficulties after the article he
and Harold Malde published. Even though Szabo, fearing negative
reactions from the findings, attempted to distance himself from the
Valsequillo project, his attempts were insufficient to escape the
disapproval of the scientific community. He encountered that censure
head-on while he was seeking a research grant for another project.
The reviewing scientist recommended the grant be denied on the basis
of Szabo’s involvement with the Valsequillo project. Szabo had been
labeled an incompetent scientist and lacked credibility
(Steen-McIntyre, personal communication with Suzanne Clark).
The process of publication is clearly a highly charged political
phenomenon. Editors of scientific journals are influential
individuals in an authoritative capacity. It is a process very
similar to the method a scientist encounters when seeking research
grants. Both are contingent upon the credentials of the individual
seeking publication or funding as well as the criteria to which the
editor adheres. The processes are equally prone to subjectivity and
Steen-McIntyre is not the only student of American archaeology to be
treated badly on the basis of her views. E. James Dixon (1993, p.
128) reports similar responses to his writings when he merely
suggested a mechanism for migration other than the Bering land
In the early 1980s I had published a
popular article on the peopling of the Americas in which I
merely hinted that humans may have colonized the Americas via
the Pacific. I was sharply and swiftly criticized by several of
my colleagues. One senior associate suggested that I not pursue
this further for fear of losing my credibility within the
It was not just Dixon’s colleagues that
found his views dangerous; editors of journals criticized his
professional writings, not because they failed to meet the journal’s
scholarly standards, but because they argued against the received
view. Dixon had done a series of studies in which he and a colleague
had grown hemoglobin crystals from material recovered from spear
points. They matched the hemoglobin from those points with that
found in living species, and also with specimens recovered from
The result was that some of those points
could be dated to well before the Clovis and Folsom barrier, as the
animals whose blood was on them were extinct before 12,000 BP. So
either humans were in America before the late Pleistocene, or these
animals survived longer than is currently supposed.
Dixon sent these
results to Science, with the following result (Dixon 1993, pp.
After Loy [Dixon’s partner in this
research] left, I went through the laborious task of editing our
article to meet the requirements of the journal, and soon it was
in the mail. About two weeks later I received word that our
manuscript had passed the first level of screening by the board
of reviewing editors and that it had been sent on to specialists
within the field for technical review. After two months had
passed, we had received no further word from the journal, so I
decided to call the editorial office. The following week I
received a letter from the editor stating that although the
reviewers had unanimously recommended publication, they would
not publish the article.
In other words, there was no complaint
about the article on either stylistic or technical grounds, but only
about the conclusions for which he argued.
This kind of reaction to anomalous evidence is, as Meltzer
says, understandable, but it also sounds quite contrary to the
spirit of science. And yet it is a common response to anomalies.
only in archaeology, but in every other science as well, challenges
to the received view are treated with exaggerated suspicion. It is
entirely reasonable to treat anomalies with suspicion. After all, if
a piece of evidence comes to light that is inconsistent with a
well-grounded theory, it is not always clear which of the two has to
Frequently, apparent anomalies evaporate
on further examination. There is some incentive for scientists to
try to overturn received theories, and so they may overstate what
their evidence shows. If a received theory is backed by lots of
evidence, it would be irrational to abandon it at the first
anomalous finding, even if there is no alternate explanation
available for the anomaly.
But what has happened to dissenters in the archaeology of the
Americas - especially those who dealt with the Hueyatlaco
evidence — goes beyond mere suspicion. Their data are treated with
contempt, their results (even when they are modestly stated) are
treated as crackpottery, and they are sometimes accused of
incompetence or dishonesty.
Why these extreme reactions?
In every science, anomalies
are met with this same hostility. It seems to be standard
practice in science, and yet it sounds paradigmatically
unscientific. The reason this is hard to square with our notions of
science is that we are failing to see science as the socially
embedded practice that it is.
Science seems to be an abstract method of theory choice, which is
immune to abuse. At the same time, science seems to be a social
practice, subject to all the abuses any human institution is subject
to. These claims cannot both be true, and yet both seem plausible.
It does seem that the scientific method (insofar as there is a
single method) is designed precisely to root out error and tend
toward truer and truer pictures of the world. On the other hand,
scientists are people, and scientific investigation is done by
people in societies, and it would be amazing if they didn’t bring
their biases into the laboratory with them.
We have three choices:
we can endorse
the first view and reject the second
we can endorse the second view
and reject the first
we can find a way to reconcile the two
In fact, the two view are indeed compatible. When the
proponents of the self-correcting nature of science say “Science is
unbiased” and the proponents of science as an ideologically driven
enterprise say “Science is biased,” they are not disagreeing,
because they are talking at cross-purposes; they mean different
things by the word ‘science’.
The former are talking about a method
employed in theory choice, abstractly conceived; the latter are
talking about a socially instantiated practice that has theory
choice as a component. Consequently, it is possible for the
abstractly characterized method of theory selection to be
self-correcting, and yet be embedded in a larger practice which to
some extent undermines, or even defeats, self-correction.
This distinction between science as theory-choice procedure and
science as social practice is easily confused with another, related
distinction, the distinction between good and bad science. For
example, many scientists would admit that particular scientists may
have let bias creep into their work, but that when they were doing
so, they were doing bad science. In other words, it is ideal
science, or good science, that corrects itself. But both sides to
the debate can agree that there is good and bad science.
The believers in science may admit that
some scientists are biased, but they want to assert that it is not
merely in the ideal that science corrects itself, but also in real
practice. They want to claim that science as we actually do it has a
tendency toward truth, which would be unwarranted if it were only
science as ideally practiced that has that feature. Also, many of
the political critics of science want to claim that even when
science approaches the ideal of objectivity, it still serves
political power. So the distinction between real and ideal science
does not illuminate the problem.
The defenders of the objectivity and self-correcting nature of
science think of science as a method, structurally designed to weed
out error. In particular, it is meant to weed out error due to the
personal perspectives of scientists. The scientific method, as
described in innumerable science textbooks, is something like this:
a hypothesis is conceived, it doesn’t matter how
consequences of that hypothesis are deduced
designed to see if those consequences are true
if not, the
hypothesis is proven wrong, and the process returns to the
beginning, with a revised or completely new hypothesis
consequences are correctly deduced, and the experiments are
well-designed and well-performed, then the original hypothesis is
refuted, even if it was the pet hypothesis of a well-beloved and
Richard Feynman (1990, p. 156) describes the method this way:
In general we look for a new law [of
physics] by the following process. First we guess it. Then we
compute the consequences of that guess to see what would be
implied if this law that we guessed is right. Then we compare
the result of the computation to nature, with experiment or
experience, compare it directly with observation, to see if it
works. If it disagrees with experiment it is wrong. In that
simple statement is the key to science. It does not make any
difference how beautiful your guess is.
It does not make any difference how
smart you are, who made the guess, or what his name is — if it
disagrees with experiment it is wrong. That is all there is to
it. It is true that one has to check a little to make sure that
it is wrong, because whoever did the experiment may have
reported incorrectly, or there may have been some feature in the
experiment that was not noticed, some dirt or something; or the
man who computed the consequences, even though it may have been
the one who made the guesses, could have made some mistake in
Feynman goes on to say that this picture
is a bit oversimplified, but his further remarks only serve to add
details to the three-part structure: hypothesis, deduction,
experiment. The results of the experiment then have an effect on
what hypotheses get proposed, so the process is a self-correcting
spiral, homing in on accurate representation of the world. It is
easy to see how this understanding of science would lead one to
think that it could not possibly be biased. If a biased scientist
presents a faulty hypothesis, it will not be borne out by
experiment; and so bias is rooted out, at least in the long run, by
the structure of science itself.
The critics of science as we now practice it do not see science as
this idealized and highly abstract method of theory choice. The
classical “scientific method” is a component of science, but it is
not the whole thing. They are thinking of science as a social
practice that starts well before hypothesis with background
information, distribution of resources and opportunities, and ends
with publication and discussion of theories. What theories are
accepted, published, and discussed forms the new background
information out of which new hypotheses arise, so on this picture,
too, science spirals, but the spiral is guided by more than just
observation and experiment. It is because of these additional forces
on scientific inquiry that science (in the “practice” sense) can be
biased, even if science (in the “method” sense) is immune to bias.
Science as a social practice can be broken down into three stages:
hypothesis selection, theory choice, and theory uptake.
Theory choice has been the focus of much
discussion of science, and so has become science itself for so many
people, because it is amenable to abstract treatment. In particular,
it is amenable to a normative understanding; understanding science
as theory selection allows us to develop logics of science, and
interpret particular cases of theory selection in terms of how well
they achieve the goals of science, including an accurate picture of
the world. But obviously there is more to how science gets done, and
more to what scientific theories we accept, than the logic of theory
choice alone. The scientific practice, as actually undertaken by
real, working scientists, is better represented as a three-stage
structure, with theory choice taking place in a context of
hypothesis selection and public uptake.
At the stage of hypothesis selection, science gets its direction. To
begin with, what science gets done is partly a function of what
previous scientists have already done and what presently employed
scientists would like to see done. Scientists are partly hired,
promoted, and otherwise evaluated on the strength of how interesting
the problems are that they are pursuing, so what we find out about
the world is in part a function of what presently employed
scientists find interesting. Proponents of theories that postulate a
pre-Clovis human presence in the Americas will (as Steen-McIntyre’s
case shows) have trouble finding employment.
Hypotheses that no one respects will
have trouble finding funding and support; hypotheses that are very
radical will be difficult even to formulate, for lack of a history.
So, what theories we accept is constrained by what hypotheses get
tested. At the theory-uptake stage there are similar constraints. If
no scientific society or journal finds your work important or
interesting, it won’t get published, and so other scientists will
not try to replicate the results, and the general public will never
find out about it. A lot of evidence against the standard view gets
weeded out at this stage (as Dixon’s case shows). Evolutionary
biology had to wait decades for Gregor Mendel’s
groundbreaking work because it languished in a second-rate journal
that nobody was reading.
Even if a paper on a problem considered
marginal by the majority makes it to publication, if the scientific
community doesn’t pick up on it, discuss it, and expand on it, it
vanishes into obscurity. So while we confine ourselves to
consideration of the scientific method, it is true that any
hypothesis, no matter what it is or who brings it up, is treated
equally, when we turn to the social practice of science, we see that
only hypotheses that can attract enough interest to get resources,
publication, and discussion really have a chance to be accepted.
These two ways of looking at science give us another way to draw
Kuhn’s distinction between normal science and scientific revolution,
without his flirtations with anti-realism. When there is an accepted
theory in place (a “paradigm”, if you like), there are
well-structured alternative research projects, developing different
aspects of the received view. Scientists who undertake different
research projects see each other as all doing respectable work, even
if they are mutually inconsistent.
Scientists who undertake projects
outside the well-structured set of alternatives (like flat-earthers
or creation scientists) are dismissed as crackpots. Scientific work
that is within the pale of respectable work is then evaluated solely
on the grounds of how well it meets the canons of science in the
“method” sense. Anything respectable as determined by the received
view will be accepted as worth doing, and will have a chance at
publication and funding. The middle stage of theory choice looms
large, and the forces that operate on problem selection and theory
uptake have little work to do. In a time when evidence is turning up
that calls a received view into question, the line between
crackpottery and respectable science is temporarily blurred.
As a result, the first and third stages
of the scientific enterprise take on a larger role. If it is no
longer clear (except in extreme cases) who the crackpots are and who
the good scientists are, the question of who gets hired, who gets
funded, and who gets published will have a correspondingly larger
effect on the resulting science. Also, without clear criteria for
distinguishing between good science and bad, the criteria actually
applied will be more prone to subjective bias.
Unfounded charges of incompetence or
fraud will be much more common, and more injustices will be done.6
We get this classification of
evidence from Meltzer 1993, pp. 84-94.
A full elaboration of this evidence
and what it implies is to be found in Greenberg 1987.
The complete team consisted of Dr.
Cynthia Irwin-Williams, archaeology, Principal Investigator,
Professor Juan Armenta Camacho, archaeology, Dr. Virginia
Steen-McIntyre, tephrochronology, Dr. Harold E. Malde, geology,
Dr. Clayton E. Ray, palaeontology, Dr. Dwight, malacology, R. B.
Taylor, Dr. Gordon Goles, neutron activation analysis, Mr. Mario
Pichardo del Barrio, palaeontology.
Identifying the source of the
volcanic pumice and ash proved to be difficult. Additional
samples were later collected by Steen-McIntyre and Fryxell, some
of which were later compared to fragmentary samples taken from a
volcano, La Malinche, near the site. None of the samples proved
to be identical to the La Malinche samples. Two layer samples
did look similar, but not identical as expected. The glass and
crystals in the pumice lumps produced from the Tetela Brown Mud
looked very different. See Steen-McIntyre, Fryxell, and Malde,
1981, pp. 1-17.
Irwin-Williams’s championing of this
date is particularly puzzling, since it is both too late for the
physical evidence at Valsequillo (which points to an age an
order of magnitude higher) and too early for the larger body of
indirect evidence (which points to a date 10,000 years later).
We are grateful to Virginia
Steen-McIntyre for a great deal of information regarding the
Hueyatlaco dig. Thanks are also due to George Agogino of Eastern
New Mexico University, for giving us access to the personal
papers of the late Cynthia Irwin-Williams.
Dixon, E. James (1993) Quest for the
Origins of the First Americans. Albuquerque: University of New
Feynman, Richard (1990) The
Character of Physical Law. Boston: MIT Press.
Greenberg, Joseph (1987) Language in
the Americas. Stanford: Stanford University Press.
Haag, William G. (1973) “The Bering
Land Bridge” in Early Man in America. San Francisco: W. H.
Freeman and Company, pp. 11-18.
Irwin-Williams, Cynthia (1967ª)
“Associations of Early Man with Horse, Camel, and Mastodon at
Hueyatlaco, Valsequillo (Puebla, Mexico)” in Pleistocene
the Search for a Cause. Edited
by P. S. Martin and H. E. Wright. New Haven: Yale University
Press, pp. 337-350.
(1967b) “Comments on Allegations
by J. L. Lorenzo Concerning Archaeological Research at
Valsequillo, Puebla” in Paleo-Indian Institute, Eastern New
Mexico University Miscellaneous Publications, Number 1,
(1969) “Comments on the
Associations of Archaeological Materials and Extinct Fauna
in the Valsequillo Region, Puebla, Mexico” in American
Antiquity 34: 82-83.
(1978) “Summary of
Archaeological Evidence from the Valsequillo Region, Puebla,
Mexico” in Cultural Continuity in Mesoamerica. Edited by
David L. Browman. The Hague: Mouton Publishers.
Kuhn, Thomas (1970) The Structure of
Scientific Revolutions. Chicago: University of Chicago Press.
Lorenzo, Jose L. (1967) “Sobre
Metodo Arqueologico” in Boletin of the Instituto Nacional de
Antropologia e Historia, Junio.
Malde, Harold E. and Virginia
Steen-McIntyre (1981) “Reply to Comments by C. Irwin-Williams:
Archaeological Site, Valsequillo, Mexico” in Quaternary Research
Meltzer, David J. (1993) Search for
the First Americans. Washington: Smithsonian Books.
Steen-McIntyre, Virginia (1980)
“Approximate Dating of Tephra.” Presented at NATO Advanced
Studies Institute on Tephrochronology, Iceland, June 1980.
Steen-McIntyre, Virginia, Roald
Fryxell, and Harold E. Malde (1981) “Geologic Evidence for Age
of Deposits at Hueyatlaco Archeological Site, Valsequillo,
Mexico” in Quaternary Research 16:1-17.
Szabo, Barney J., Harold E. Malde,
and Cynthia Irwin-Williams (1969) “Dilemma Posed by
Uranium-Series Dates on Archaeologically Significant Bones from
Valsequillo, Puebla, Mexico” in Earth and Planetary Science
Turner, Christy (1986) “The First
Americans: the Dental Evidence” in National Geographic Research