Warning: ca 11 pages
I'll assume everyone whose interested knows the history of this. So no
explanation this time.
This is my response to Jonathan Wells's remarks on our discussion of
peppered moths, posted to the Calvin Evolution group on 4/06/99 by Art
Chadwick. I assume Art will again get a copy to Wells.
> Don Frack's strongly worded disagreement with my assessment of
> the peppered moth story highlights a number of issues.
Lest anyone forget, the following quote is what I found offensive. It
relates directly to my concerns about the use (or abuse) of Jerry Coyne's
book review of Michael Majerus's book by creationists to attack public
school textbooks. The question is whether Wells can justify his original
extreme claims with unqualified facts. If he had taken the tone of his
recently published web article, I would have little to say. But I am not
sure whether the more measured tone this time indicates Wells was having a
bad day before or that he is being more political now.
"BUT EVERYONE, INCLUDING MAJERUS, HAS KNOWN SINCE THE 1980'S THAT PEPPERED
MOTHS DO NOT REST ON TREE TRUNKS IN THE WILD. This means that every time
those staged photographs have been knowingly re-published since the 1980's
constitutes a case of deliberate scientific fraud. Michael Majerus is
being dishonest, and textbook-writers are lying to biology students. The
behavior of these people is downright scandalous."
"Fraud is fraud. It's time to tell it like it is."
I apologize for the delay in posting this, reading and evaluation take time,
and the rent must be paid.
I made an error in my previous message, that Wells has brought to my
attention. I stated in an addendum to explain an accompanying message sent
to me by Michael Majerus that Wells had substituted the word "precised" with
the word "basic". I was wrong and I beg his pardon.
However, I was attempting to draw the readers' attention to what Majerus
himself was complaining about in Wells's text. I had just received this
message before posting mine, and tried to clarify to the reader what the
problem was. I think Wells understands clearly how I made the mistake, as
focus on the word "precised" should indicate. He took tactical advantage
without even acknowledging that Majerus's complaint was genuine. Majerus
left out the word "basic" in his email and in trying to briefly describe the
situation I mistook the literal problem. The complaint by Majerus arose from
Wells removing the subject of the sentence ("precised description") in
editing it, leaving an erroneous interpretation based on the subject's
modifier. My reminder "never to trust a creationist quote" still applies.
The claim, as Wells puts it, of "poor and/or dishonest scholarship" was
Wells repeatedly makes me an advocate for Michael Majerus. I am unaware
that I ever "sided" with Majerus contra Sargent. My only comments were to
the facts that Wells wrote as if there was wide support for his views, but
he, and his colleague Paul Nelson in defending his views on the Calvin
forum, relied repeatedly on Sargent et al or a previous paper by its other
two co-authors. This was to point out Wells's narrow use of references, and
said nothing about the value of Theodore Sargent's work.
I got into this situation because I wrote an evaluation comparing Jerry
Coyne's book review with Majerus's book itself. Everyone had assumed that
Majerus himself held the views described in the review. I showed that this
was not the case, and got verification to that effect from Majerus, who I
did not know. I do not understand then how Wells can conclude "Coyne found
himself unpersuaded by Majerus's defense" when I had to show that Coyne's
version did not represent Majerus's views. Everyone I know of thought Coyne
and Majerus were in agreement. Since Wells claims he is relying on actual
evidence, what justification is there for hiding behind Coyne as an
> Since experts such as Sargent and Majerus disagree over the interpretation
of the data,
> perhaps we should go to the original papers.
I couldn't agree more.
> The main point, it seems to me, is that research conducted in the 1980's
> shows quite clearly that peppered moths do not normally rest on
> tree trunks
> in the wild. At the risk of belaboring the point and trying readers'
> patience, here is an excerpt from the review I wrote last year:
I note for Wells that he has put his article on the Web (True.Origins) the
same day I received the post I am responding to here (end of Wells article
plug). I would be interested in getting the citation for where this 1998
article was originally published, since it is not given here and I would
like to add it to my recently bloated peppered moth literature collection. I
note that we are now talking about whether or not the moths "normally rest"
on trunks, whereas Wells's original claim was that they DO NOT rest there.
The difference is support for the extreme claims Wells made against anyone
who shows the moths on tree trunks in photos, etc.
Hoping not to risk the readers' patience any more than Wells, I repeat his
statements in full for comparison to what I will say about its contents.
Please note especially that the bulk refers to Mikkola (1984), with later
support from other authors.
> from SECOND THOUGHTS ABOUT PEPPERED MOTHS
> by Jonathan Wells (1998)
> ....Since 1980, however, it has become clear that
> peppered moths do
> not normally rest on tree trunks. Mikkola observed that "the normal
> resting place of the Peppered Moth is beneath small, more or less
> horizontal branches (but not on narrow twigs), probably high up in the
> canopies, and the species probably only exceptionally rests on tree
> trunks." He noted that "night-active moths, released in an illumination
> bright enough for the human eye, may well choose their resting sites as
> soon as possible and most probably atypically." Thus "the results of
> Kettlewell (1955, 1956) fail to demonstrate the qualitative predation of
> the morphs of the Peppered Moth by birds or other predators in natural
> conditions." (10)
> Mikkola used caged moths, but data on wild moths support his
> conclusion. In twenty-five years of field work, Clarke and his colleagues
> found only one peppered moth on a tree trunk, and admitted that they knew
> primarily "where the moths do not spend the day." (11) When Howlett and
> Majerus studied the natural resting sites of peppered moths (Biston
> betularia) in various parts of England, they found that Mikkola's
> observations on caged moths were valid for wild moths, as well, and
> concluded: "...it seems certain that most B. betularia rest where they are
> hidden.... [and] that exposed areas of tree trunks are not an important
> resting site for any form of B. betularia." (12) In a separate study,
> Liebert and Brakefield confirmed Mikkola's observations that "the species
> rests predominantly on branches.... Many moths will rest underneath, or on
> the side of, narrow branches in the canopy." (13)
> In a recent book on melanism, Majerus criticizes the
> "artificiality" of much previous work in this area, noting that "in most
> predation experiments peppered moths have been positioned on vertical tree
> trunks, despite the fact that they rarely chose such surfaces to rest upon
> in the wild." (14)
[references snipped, see Wells's original]
> [Regarding the above: Clarke and his colleagues actually found TWO
> peppered moths resting in the wild in their 25 years of field work. Frack
> notes sarcastically that "Wells has lost a moth" because I cite only one;
> but if Frack had consulted the original paper by Clarke et al. he would
> have learned that one of their two moths was found resting on a fence, not
> a tree trunk.]
Wells admonishes me [above] to consult the original paper by Clarke et al.
Although I suspected that this was his reference (I noted Coyne's similar
statement in my first [pre-Wells] discussion of the subject), I confess my
crystal ball failed me here. I would only ask Wells how I was supposed to
know that he was referring the Clarke when no such connection exists in his
text? Wells's entire text is "In 40 years of field work, only one peppered
moth was found resting on a tree trunk in the wild." No reference is cited
there. Wells also puts his own (possible) interpretation on Clarke's words.
I quote Clarke completely later, but I note here that the actual reference
states vaguely that the two moths were found on "tree trunks or walls
adjacent to our traps (one on an appropriate background and one not)". Note
throughout Wells arguments how often this one vague, probably anecdotal
sentence is used.
Here are my observations on the references and extracts used by Wells.
Wells claims to be an objective scientist just evaluating the evidence, not
affected by preconceptions especially natural selection. Note that he gives
special importance to Mikkola's cage experiments. Discussions on each paper
discussed by Wells are headed in UPPER CASE.
"Biston" and "B. betularia" refer to peppered moths.
"Selective coefficient" is a calculation for mathematical modeling, etc.
Frankly, I was surprised (not positively) when I saw the photo of Mikkola's
cage setup and discussion in the text. The cage consisted of a one meter
high plastic cylinder, about the size of a 50 gallon trash can. Two 5"
diameter trunks reached from floor to ceiling with six smaller horizontal
"branches" attached to each at right angles. The wood was spray-painted
light and dark on opposite sides for behavior experiments. This was hung at
about waist level from a tree. Moths were released into the cage about 16
per day for resting position observations.
Please note Mikkola's own complaints about the design of the cage, and
unexpected behavior of the moths.
"The cage was originally designed to provide data about the choice by Biston
of horizontal and vertical pieces of wood. However, this partly failed
because the trunks touched, or were too close to, the roof and the floor of
the cage. Many Peppered Moths simply walked up the trunks from the floor or
settled at the top of them, apparently without performing any particular
background choice. Most attention was therefore paid to the moths resting
on the horizontal branches, the majority of which certainly had alighted
from flight (see below) and supposedly showed the proper resting behaviour."
Mikkola's data table totals were:
Branches:77 [40%]; Trunks:51 [27%]; Other (elsewhere in the cage): 63 [33%];
His conclusion, set off in a one sentence paragraph (and excluded the
"Other" category), is:
"In spite of the walking of the moths to the trunks, the branches collected
arithmetically more moths: 51 [40%] and 77 [60%] respectively." (p. 414,
Mikkola's conclusions are based on a 60% branch/40% trunk split, with all
the problems noted here by the author.
Various parts of the **second** sentence following are often cited from
"Their preference for horizontal branches over vertical trunks was also
evident but could not be statistically shown because of the design of the
experimental cage. It seems clear that the normal resting place of the
Peppered Moth is beneath small, more or less horizontal branches (but not
narrow twigs), probably high up in the canopies, and the species probably
only exceptionally rests on tree trunks." (p. 416)
I find it less than obvious how the conclusion "high in the canopy" follows
from the experiment, or how it shows the moths do not "normally" (in any but
a possibly statistical sense) rest on trunks. The results are, to use the
euphemism, "suggestive" for later researchers attempting to improve
selective coefficient calculations. I don't understand why Wells himself is
so impressed with a 60/40 split. Mikkola, however, was *convinced* that the
moths were higher up in the trees.
CLARKE ET AL 1985
I note that these authors do not support Mikkola's views. The case is quite
the opposite. Howlett and Majerus (next reference) interpreted this as
support for trunk-resting.
"But the problem is that we do not know the resting sites of the moth during
the day-time. Mikkola (1984) states that they settle on the upper branches
of trees and he shows a photograph of a typica moth in this situation
against the camouflage of a white lichen. We do not believe that this type
of protection occurs in our area and all we have observed is where the moths
do *not* spend the day. In 25 years we have only found two betularia on the
tree trunks or walls adjacent to our traps (one on an appropriate background
and one not), and none elsewhere." (p. 197)
HOWLETT & MAJERUS 1987
I include here extracts from this paper to show that the issue was a problem
of mathematical models that do not correspond properly with observed data.
Different authors proposed suggestions that might improve the
correspondence. Howlett and Majerus advocated that if the statistically
"normal" resting site was higher in the trees the selective coefficient
would be lower (the moths wouldn't be as obvious).
Abstract: "The results of a pilot selection experiment, while agreeing
qualitatively with Kettlewell's results, suggest that fitness estimates that
assume trunk-resting are quantitatively incorrect. The error is greatest
for melanic moths in rural areas. It is suggested that visual selective
coefficients based on a true assessment of the resting behaviour of the
moths may considerably improve the fit between computer predictions and
observed frequency distributions." (p. 31)
"In this paper we consider some of the evidence put forward to explain the
relative frequencies of melanic and non-melanic forms of this species. We
question the visual selection coefficients obtained from predation
experiments which assume that the moths habitually rest in exposed positions
on tree trunks. We note the poorness of fit between observed frequencies
and models using selective coefficients based on independent experiments."
"Mikkola's observations of the moths in experimental cages may help to
explain the discrepancies between model-predicted and observed morph
frequencies." (p. 36)
"Although Clarke et al question the importance of aspects of the
microenvironment, they do not appear to doubt that the moths habitually rest
on tree trunks. Yet they themselves state that 'in 25 years we have only
found two B. betularia on tree trunks or walls adjacent to our traps, and
none elsewhere.' In fact the evidence for where B. betularia rest during the
day in the wild are slight." (p. 37) [Note that Clarke et al are viewed as
the opposing opinion.]
"Although there can be no doubt that the species does occasionally rest on
tree trunks in exposed positions, the few observations of resting B.
betularia that one of us has made in 20 years of moth hunting lead us to
believe that exposed tree trunks are not the primary resting site for this
species." (p. 37)
"Our findings and those of Mikkola are not original. Kettlewell (1958b)
makes the most remarkable statement '... whilst undertaking large-scale
releases of both forms (of B. betularia) in the wild at early dawn, I have
on many occasions been able to watch this species taking up its normal
resting position which is beneath the larger boughs of trees, less commonly
on the trunks.' Although we do not know whether Kettlewell was watching
moths take up 'normal resting positions' we feel it pertinent to note that
Kettlewell recognized trunks as a less commonly used resting site."
Since Wells does not seem to look favorably on selection, it is interesting
that he doesn't consider these authors' views, which are clearly influenced
by the need to correct theoretical models of selection, as bogged down in
LIEBERT & BRAKEFIELD 1987
Wells describes/quotes from the Abstract of this paper (quoted directly
"Our observations support Mikkola's earlier conclusion from cage experiments
with male moths that the species rests predominantly on branches and shows
an appropriately specialized resting attitude, demonstrated here in a series
of photographs." (Abstract; p. 129)
The only problem I have with Wells's decision to quote the Abstract (which
is essentially correct), as opposed to the main text itself, is it leaves
out the qualification and the additional last word in the actual article
text, which seems to me to be of some interest under the circumstances:
"Overall, our observations of pairings and females moths suggest a more
varied choice of resting position that proposed by Mikkola (1984). Some
will rest on main branches or **trunks** (see Howlett and Majerus, 1987)."
(p. 145, **emphasis** mine)
The authors fully recognized that the trunk/canopy issue was one of relative
fitness calculations compared to the whole range of potential resting sites
of the moths, and that these calculations might be too high based on trunk
predation studies alone:
"We agree with Makkola's critique of field experiments to estimate the
relative fitness of the phenotypes of B. betularia by using moths exposed on
tree trunks. Such predation experiments must take into account the full
range of the moth's resting sites in more, or less exposed positions." (p.
These researchers were aware that the exitsting experimental predation data
from tree trunks reflected only part of the probable diversity of resting
sites of the moths. Correct estimation of selective coefficient values for
models required a reevaluation based on that fact.
Kettlewell himself was aware of the problem that the "normal" resting site
of the moths was probably in the canopy, but since it was work where you can
reach (trunks and *boughs*) or not work at all - he chose to work. From his
first paper that I have seen:
Kettlewell, B. 1955. "Selection experiments on Industrial Melanism in the
Lepidoptera", Heredity, 9:323-342.
"I am not aware of previous attempts to discover the selective advantages of
melanic insects by mark-release recapture experiments. To the obvious
criticism that the releases were not free to take up their own choice of
resting site for the first day, I must answer that there were no other
alternative backgrounds available for an insect that has to spend its days
on trunks and boughs in this wood. I admit that, under their own choice,
many would have taken up position higher in the trees, and that since the
surface area of a tree increases proportional to the distance up the trunks
and boughs, in so doing they would have avoided concentrations such as I
produced. Tinbergen (1952), de Ruiter (1952) and others have shown the
importance to cryptic insects of avoiding too high a density level, but this
is no argument against the findings for the *relative* advantages of the
three forms. It must be accepted, however, that, under natural conditions,
predation, though selective, might take place at a lower tempo." (p. 340,
*emphasis* in original)
The last comment, published in 1955, is what researchers were trying to
correct in the 1980's. Kettlewell's "lower tempo" refers to the same issue
as changing "visual selective coefficient."
Before being dazzled (or bewildered) by the numbers in Wells reanalysis of
Majerus's data tables I presented previously, the first point was that Wells
left Majerus's data out ENTIRELY. On the other hand, Clarke's single
sentence, probably anecdotal, is quoted again and again. I reproduced the
actual tables to show that they were clearly displayed by the author(s). I
keep finding recent critics like Wells simply ignoring the single most
famous work on the subject (cited in at least 12 subsequent papers I have),
and Majerus's recent book that updates it. Three recent critics have use
Clarke (cited or abstractly) and ignored Majerus.
Now that I have seen Majerus's original table published in 1987, I must
correct an earlier error. Majerus's book uses the table style from his
earlier 1987 work but does not clearly describe the difference between
"exposed trunks" and "unexposed trunks." From the context, I surmised he
meant the trunk hidden in the canopy. This is incorrect. The category
"unexposed trunks" is explained by describing the two specimens originally
in it, in the original 1987 paper. The category refers to specimens on
trunks that are not clearly visible to predators. The text states "In the
case of the two moths in unexposed positions on trunks [refers to data
table, DF], one was hidden behind ivy on Douglas fir, the other on a birch
trunk behind foliate twigs sprouting from a knot just below the moth." (p.
39) The two trunk categories therefore should be combined for purposes here,
since Wells original contention was that the moths do not rest on trunks at
all (see his original posting, "BUT EVERYONE, INCLUDING MAJERUS, HAS KNOWN
SINCE THE 1980'S THAT PEPPERED MOTHS DO NOT REST ON TREE TRUNKS IN THE
WILD.", CAPS in original). Majerus's table therefore lists about 25% of the
specimens from trunks. Wells fidgets over one, two or six moths. Even with
his incessant ONE moth, it's one of one on a trunk. I think readers will be
far less impressed with "one moth in 40 years" if they know that it's the
only one claimed to have been found by the authors, period. Either we look
at the representation compared to sample size (e. g. percent of total), or
the numbers don't mean a thing and will mislead the public Wells says he
wants to defend.
I agree completely with Wells that the total data are "underwhelming." My
conclusion from the literature, which surprises me as much as anyone, is
that I've seen no record that anyone other than Majerus has made organized
attempts to resolve the problem. Wells "intense research" comment is not
supported by anything I have seen that justifies it. I would be surprised if
there are not data somewhere collected by someone. But I haven't seen
reference to them, and I would think Majerus would have listed any
significant collections he knew of.
Since I don't believe what has been called a "mystery" of the moths' resting
place is due to something like that they teleport to/from another dimension,
then they are out there to be found. I, and many of my fellow insect
collectors, have found "rare" insects to be common once someone actually
went looking for them seriously. The fact that peppered moths may occur at
low densities and the fact that they are cryptically colored makes it
understandable that it may take truly dedicated work to get very many
specimens. The payback for the effort may be very small. Kettlewell
designed grading scales for degrees of crypsis, and was clearly an
experienced observer of peppered moths. Yet he abandoned some methods of
evaluation that relied on refinding specimens placed on trees because he
discovered that he couldn't always find them again.
Majerus is almost certainly right that the normal (in the statistical sense)
resting position is higher up, but realize we are now talking about
statistical probability not absence as Wells originally contended. Are we
going to say textbook authors are "lying to their students," as Wells
originally did, because a photo was taken more than, for example, one
standard deviation from the mean resting site?
> Although these data add to Clarke et al.'s 1985 report of finding only one
> trunk-resting moth in 25 years of field work, they confirm the conclusion
> that peppered moths do not normally rest on tree trunks in the wild.
> Although a small percentage of moths do so, at best this makes cryptic
> coloration and selective bird predation a possible (but minor)
> contributing factor in industrial melanism.
Clarke's comment does not have the significance Wells repeatedly gives it.
It could only confirm that there has been too little effort put into finding
the resting location of the moths, unless some indication is given of the
effort expended. Wells is content to call ignorance knowledge, I am not. He
repeatedly uses the same citation as gospel, whereas the only evidence I
have seen indicates that it is simply anecdotal and not based on field work.
Clarke's fame relies on collections of trapped moths from around his home.
This does not demonstrate that he looked seriously for resting moths. If
Wells has reference to such relevant field work by Clarke or his immediate
colleagues, I would appreciate the citation.
Wells contention that cryptic coloration and selective bird predation are
"possible (but minor)" is contrary to everything I have seen published by
established researchers. This appears to be Wells own personal view. He
seems to rely on a logic that birds don't go into the tree canopy, or that
cryptic coloration has no effect there. If he means that moving the "normal"
resting site means there is no evidence for bird predation, I suggest he
reread Majerus's 1987 and 1998 works (the pilot selection study mentioned in
the quotes from the 1987 paper, above) and Liebert and Brakefield 1987
(simple observation that birds ate their specimens).
> Frack follows Majerus in discounting the possibility that direct
> rather than natural selection, was responsible for industrial melanism in
> peppered moths. Heslop Harrison claimed in the 1920's that
> induction could
> account for melanism in other insect species (he didn't work on peppered
> moths), but others investigators were unable to replicate his work. Some
> biologists (such as Thedore Sargent) continue to maintain that
> induction is
> still a theoretical possibility. Personally, I am not arguing for
> induction, but merely pointing out that natural selection is not the only
> conceivable possibility (unless one is a dogmatic Darwinist). I remain
> skeptical of induction; but recent evidence has also made me skeptical of
> selective bird predation. Any scientist interested in
> discovering the true
> cause(s) of industrial melanism would presumably be wise to remain open to
> more than one possibility.
Wells should teach creative writing. He says I "follow Majerus" regarding
induction. I do not. I am not aware that induction and Majerus are ever
joined in my text. What I did point out was that Wells (and his colleague
Paul Nelson) constantly relied on *one* reference (and a preceding paper by
two of the same authors), while giving the appearance of broad support. That
is a simple observation of the use of literature. I commented on the history
of induction from Sargent et al directly, pointing out that rejection of
induction occurred before Kettlewell's research, contrary to what Wells
claimed. Nowhere have I denied induction as a "theoretical possibility."
Nowhere have I claimed that natural selection is the only possibility. I am
skeptical of induction, as Wells himself says he is. That is simply because
it is outside my experience that physically induced changes can become
genetically fixed. That's based on my background as a biologist, period. I
also noted previously that supporters of induction have not shown evidence
in its favor. If anyone presents it, I'll consider it. I have no particular
opinion one way or the other.
For someone who is skeptical of induction, Wells sure is pushing it. He
associates others' skepticism of induction with being "a dogmatic Darwinist"
in BOTH of his texts. It looks like Wells may be pumping this because he
himself is "a dogmatic ANTI-Darwinist" and has some reason for pushing the
issue. I address this question at the end here and in the accompanying
"Peppered Moths and Creationists".
I thought Wells had decided that staging specimens for illustrative
photographs was not the issue, but now here it is. I have not denied, but
rather emphasized that I expected many book illustrations were staged, so
there is little point in commenting on most of this again. I've already
covered it in detail. But, as long as we're going to purge biology books,
let's do it right. That gibbon picture actually shot in the San Diego Zoo
is an obvious fraud! The peppered moth one may be off by a few feet of the
"normal" position, but this one's not even on the right continent. And
those protozoans... We MUST show the fraud that they do not normally live on
microscope slides where they were photographed!
I was unaware until just now that bird predation was an issue. Since when
was there doubt among peppered moth researchers on this point? I thought
Wells hot button was tree trunks, but it appears he's ... branched out.
> On a personal concluding note, I would like to add that my objections to
> the textbook peppered myth have nothing to do with creationism, despite
> Frack's repeated attempts to discredit me with that label. Even if the
> classical peppered moth story were 100% accurate, it would pose no threat
> to creationism -- including the young-earth variety -- so why would anyone
> oppose it on "creationist" grounds anyway?
So, is he is or is he ain't a creationist? We're finally down to it. This
paragraph is addressed in the accompanying document "Peppered Moths and
Wells gives a speech here that seems a little too soapboxish to bother
anyone with. Since this is being posted to a discussion group of people
whose analysis powers I respect, I leave it to them to determine the value
of Wells's personal concluding notes.
> Is "creationism" versus "evolutionism" at issue here? If it is, it's not
> because I brought it up. If Frack thinks it is, perhaps he should explain
I'm sooo glad Wells said this. Please see the accompanying "Peppered Moths
For those willing to suffer a little more, I have one last topic. Has anyone
wondered why Wells has such a fetish for induction, since he says he's
skeptical of it? Why not other possibilities? And why, as I've pointed
out, did he relied so heavily on "Sargent et al" in his first response? His
colleague Paul Nelson carried the cause in this discussion group quoting
Sargent et al extensively, as well as a previous paper by its two
It is commonplace in anti-evolution lectures and literature to value
conclusions of people who oppose standard interpretations of evidence
concerning evolution, regardless of what they think of the evidence itself.
Hoyle, Zuckerman, Kerkut and others come to mind. I will leave unnamed the
well known creationist lecturer who praised Hoyle to the audience, and spoke
of Hoyle's ideas in the lowest terms in private. This is the desired tail
wagging the perhaps unwanted dog.
What I have referred to in abbreviation as "Sargent et al" is actually
authored by T. D. Sargent, D. M. Lambert and C. D. Millar. The defense of
induction in that paper is supported from earlier works by the last two
authors (with others), especially a paper by D. M. Lambert, C. D. Millar
and J. T. Hughes from 1986. Wells has concentrated on Sargent vs Majerus, I
want to discuss the other two, Lambert and Millar.
I have not yet seen this 1986 paper, but it is discussed in the peppered
moth literature. At the risk of relying on a biased review, I quote from G.
S. Mani. 1990. "Theoretical models of melanism - a review", Biol. J. Linn.
Soc., 39:355-371, which gives the best description of these authors'
position that I have seen. I leave the various "regulars" of peppered moth
research in the quote for comparison. Compare the description of the
position of Lambert, Millar and Hughes (Lambert et al, below) to Wells's
presented here. The topic is developing computer models for peppered moths,
"The main feature of the model is that using the results on non-visual
selection, migration and effects of pollution from the analysis of data in
NW England, it was possible to obtain the frequency pattern over the whole
of England and Wales and to predict the changes in these patterns with time
with reasonable confidence. To us this implies that the mechanism is
Darwinian and this view is also expressed by Mikkola and by Howlett &
Majerus though they may question the accuracy of the experimentally
determined visual predation parameters. In 1959, a century after the
publication of the Origin of Species, Kettlewell (1959) wrote in a paper
entitled Darwin's missing evidence, that Darwin died in 1882 just as the B.
betularia story was emerging and hence missed the chance of witnessing the
confirmation of his ideas. This view has been attacked by Sermonti &
Catastini (1984) and by Lambert, Millar & Hughes (1986). The position of
these authors can be summarized as follows. They first quote the papers of
Mikkola and of Howlett & Majerus which argue that the experimental design on
selective predation is flawed and that the assumption of the tree trunks
being the primary resting place for the moths is not strictly valid. Thus
rejecting all the previous experiments on selective predation, they claim
that there exists no evidence for selective predation and hence that it does
not occur. Thus the story of the peppered moth cannot be explained on a
Darwinian basis. Lambert et al. (1986) take this argument one step further
by asserting that the Darwinian theory of natural selection is not a
predictive theory since it encompasses no biological law. Presumably
Mendelian segregation or genotypic evolution through the operation of
selective forces do not have claims to being laws. Lambert et al. (1986)
then propose an explanation through nuclear-cytoplasmic interaction and
structuralism. Their explanation is not a predictive model but pure
speculation. It is difficult to see how the complex patterns of melanic
frequencies observed and the decline of these frequencies with the decrease
in pollution can be explained on such speculations." (p. 369)
Now, am I the only one who feels deja vu here? Paul Nelson noted that
Lambert et al were "challenging Darwinism" earlier in the group discussion.
I assume he got this from Wells. Anything look attractive to a certain group