Environmental Research 142 (2015) 432–442

Contents lists available at ScienceDirect

Environmental Research
journal homepage: www.elsevier.com/locate/envres

On the origins of the linear no-threshold (LNT) dogma by means of
untruths, artful dodges and blind faith
Edward J. Calabrese n
Department of Environmental Health Sciences, School of Public Health and Health Sciences, University of Massachusetts, Amherst, MA 01003, USA

art ic l e i nf o

a b s t r a c t

Article history:
Received 2 June 2015
Received in revised form
16 July 2015
Accepted 17 July 2015

This paper is an historical assessment of how prominent radiation geneticists in the United States during
the 1940s and 1950s successfully worked to build acceptance for the linear no-threshold (LNT) dose–
response model in risk assessment, signiﬁcantly impacting environmental, occupational and medical
exposure standards and practices to the present time. Detailed documentation indicates that actions
taken in support of this policy revolution were ideologically driven and deliberately and deceptively
misleading; that scientiﬁc records were artfully misrepresented; and that people and organizations inpositions of public trust failed to perform the duties expected of them. Key activities are described andthe roles of speciﬁc individuals are documented. These actions culminated in a 1956 report by a Genetics
Panel of the U.S. National Academy of Sciences (NAS) on Biological Effects of Atomic Radiation (BEAR). In
this report the Genetics Panel recommended that a linear dose response model be adopted for the
purpose of risk assessment, a recommendation that was rapidly and widely promulgated. The paperargues that current international cancer risk assessment policies are based on fraudulent actions of the U.
S. NAS BEAR I Committee, Genetics Panel and on the uncritical, unquestioning and blind-faith acceptanceby regulatory agencies and the scientiﬁc community.
& 2015 Elsevier Inc. All rights reserved.

Keywords:
Risk assessment
Dose–response
Linear dose response
CancerMutation
LNT
Ionizing radiation

1. Introduction
In the course of recent assessments of the historical and scientiﬁc foundations of dose responses models, it was learned thatthe linear dose response model was deliberately promoted toadvance ideological agendas of some of the world's most prestigious radiation geneticists (Calabrese, 2008; Calabrese, 2013a,
2015a, 2015b). These individuals intentionally misled/deceived thescientiﬁc and world communities at the highest possible levels,
including in a 1946 Nobel Prize Lecture (Calabrese, 2011a; Calabrese, 2012), in their scientiﬁc publications (Calabrese, 2011b;
Calabrese, 2013b; Caspari and Stern, 1948; Muller, 1950a, 1954;
Uphoff and Stern, 1949), in their role as members of the U.S. NAS(Calabrese, 2013a; Calabrese, 2015b, 2015a) and in publications of
the NAS [BEAR Committee, Genetics Panel – (Anonymous, 1956a;
National Academy of Sciences NAS)/National Research Council
NRC, 1956). Collectively, these deceptive actions became highly
signiﬁcant when they facilitated an unchallenged and blind-faithadoption of the Linear Dose Response (LDR) model for cancer risk
assessment of ionizing radiation and later of chemical carcinogens(Calabrese, 2011b, 2013b, 2009a). The adoption of the LDR modelnFax: þ 1 413 545 4692.
E-mail address: edwardc@schoolph.umass.edu

http://dx.doi.org/10.1016/j.envres.2015.07.011
0013-9351/& 2015 Elsevier Inc. All rights reserved.

affected the magnitude of ﬁnancial resources involved in regulatory actions, toxic tort decisions and medical practices; it also
affected risk communication messages to the general public,
educational practices, governmental research funding priorities, aswell as decisions related to lifestyle and child rearing.
The impact of these deceptions has been substantial and, to thisday, they signiﬁcantly affect and dominate regulatory policies andrisk assessment practices. Since these disturbing ﬁndings were
published as a series of separate papers in diverse scientiﬁc journals, (e.g. mutation, radiation and toxicology journals) (Calabrese,2015b, 2015a, 2011c, 2012, 2011b, 2013b, 2009a, 2014a, Calabrese,014b), it has become necessary to develop an integrated and holistic version of this complex story. In addition, newly unearthedmaterials on key individuals have been discovered and incorporated herein to clarify previous historical frameworks. Finally, critical feedback recently received from reviewers, editorsand others in the research community has proven invaluable intempering the perspective and improving the content and context
of this assessment.
This paper follows an historical timeline, starting with theprofessional/scientiﬁc relationship between Hermann Muller andCurt Stern and their subsequent collaborations on ionizing radiation during the Manhattan Project. The many, and, at times, bizarre ways in which Stern tried to prevent acceptance of thethreshold model supportive ﬁndings of Ernst Caspari, a member of

E.J. Calabrese / Environmental Research 142 (2015) 432–442

the Manhattan Project team, in order to promote the LNT model,
are detailed. Muller's Nobel Prize Lecture with emphasis on his
assessment of the nature of the dose response in the low dose
range, especially in light of the Caspari ﬁndings, is critiqued,leading to an assessment of how he and Stern acted to cover up
Muller's Nobel Prize Lecture deceit via obfuscation of the Manhattan Project ﬁndings and the strikingly false subsequent statements of Muller in the scientiﬁc literature. The paper then assessed how the leadership of Muller and Stern profoundly affected
beliefs on dose response within the genetics community during
the 1950s, especially seen through the actions of the NAS BEAR I
Genetics Panel in 1956 which assured the acceptance of the LNT byfalsifying and fabricating the research record, thereby constituting
scientiﬁc misconduct at the highest possible level.

2. The Curt Stern–Hermann J. Muller connections
Previously, this author had extensively researched the historyof the non-linear (hormetic) dose–response model, its scientiﬁcfoundations and its failure to thrive and out-compete the linear
no-threshold (LNT) dose–response model during the ﬁrst half ofthe 20th century (Calabrese, 2011b, 2005, 2009b; Calabrese andBaldwin, 2000a, 2000b, 2000c, 2000d, 2000e). As a continuationof this research activity, efforts have been exerted to assess indetail the historical and scientiﬁc origins that have resulted in thevalidation and acceptance of today's LNT model. During this investigation, it became evident that the role of Hermann J. Muller
was essential to the adoption of the LNT model and needed greater
clariﬁcation.
During this assessment of Muller, interest grew in the research
activities of the Manhattan Project at the University of Rochester,
especially those under the direction of Curt Stern who employed
the fruit ﬂy to investigate the nature of the dose response in the
low dose range. Stern was of particular interest because he had along personal and professional relationship with Muller thatwould markedly impact the LNT deception story. Stern had helped
to organize the Fifth International Genetics Congress in Berlin
during the fall of 1927 (Carlson, 1981). It was at this meeting that
Muller ﬁrst presented his landmark ﬁndings on X-ray-induced
mutations in fruit ﬂies (Muller, 1927, 1928), research that would
eventually lead to his Nobel Prize in 1946 (Muller, 1946a). Later,
Muller and Stern would have a conﬂict over Muller's deliberate
failure to acknowledge a prior discovery by Stern that provided
proof for the linear arrangement of genes, an issue that was then avery signiﬁcant question in biology. Stern would challenge Muller
on this point directly via a carefully documented letter dated August 8, 1929 [American Philosophical Society (APS) (American
Philosophical Society, 1929a). Stern informed Muller that his earlier publication in Biologischen Zentrablatt (September, 1926) addressed the “theory of the linear arrangement and have speciﬁcally stated it in the title of the paper”. Stern concluded his letterto Muller with the statement that his manuscript "had been
written before your [Muller’s] ﬁrst papers about them appeared.”
Nearly six weeks later, in a letter dated October 3, 1929, Muller
would respond “I am very sorry to have omitted mention of yourwork in my discussion of translocation and not to have given you
credit for having made the ﬁrst cytological demonstration of agenetically demonstrated translocation and pointed out its signiﬁcance for the theory of linear arrangement”. He then indicatedthat he had enclosed a “carbon copy of a note I am sending in on
the subject to the American Naturalist, which I hope you willconsider as rectifying this mistake” (American Philosophical Society, 1929b). While Stern caught Muller in a signiﬁcant professional indiscretion, he let Muller “control” the narrative by not
objecting to Muller’s version of the correction. Nonetheless, this433

arrangement proved to be acceptable to Stern as seen in an October 23, 1929, letter from Stern to Muller, restoring a positive tone
to their relationship (American Philosophical Society, 1929c). One
could speculate what might have happened to the LNT story if
Muller and Stern had not reconciled, possibly preventing Muller’s
involvement in the Manhattan Project as described below.

3. The Manhattan Project: Curt Stern and LNT
After Stern1 initiated research on the Manhattan Project in1943, he contacted Muller, then a professor of biology at Amherst
College (1940–1945), to serve as a consultant to the project. Under
normal circumstances this might have been routine, but Muller
had a questionable past, abandoning the US to live and research in
the Soviet Union from about 1934–1938 (Carlson, 1981). Stern
nonetheless obtained approval by the U.S. government for Muller's
participation in the radiation genetics project. Muller's involvement proved to be extensive, involving detailed technical written
communications with Stern and other team members, visits to the
University of Rochester, and a donation of his Muller-5 strain of
Drosophila (Calabrese, 2011c).
The Manhattan Project of Stern was designed to expand thestudy of high dose ionizing radiation on genomic mutations toinclude the area of chronic, lifetime exposures at relatively low
doses and very low dose rates. The ﬁrst experiment under Stern's
direction was an acute (i.e., short duration) exposure study over abroad dose range. It was conducted by Warren Spencer, a professor
at the College of Wooster with a PhD from Ohio State University inthe area of Drosophila biology. Previous research by several of
Muller's students (Hanson and Heys, 1929, 1932; Oliver, 1930,
1931), at very high doses and over a limited dose range, provided
support for the hypothesis that the nature of the dose response for
X-ray-induced mutation was linear.
In the Spencer study, the effects of X-rays were assessed on
sex-linked recessive lethality using Drosophila with acute/shortterm (2–40 min) exposures and a dose-rate ranging from 10 to
96 r/h. This resulted in a range of cumulative doses from 4000 r
down to 25 r (i.e., lowest cumulative dose yet tested). Following adata collection period from December, 1944 to June, 1955, Spencer
reported that X-rays induced gonadal mutations in a manner thatwere linear across the dose response continuum, just as Stern andMuller had predicted (Calabrese, 2011c).
Ernst Caspari, a Ph.D. in insect behavior, directed the next
study. From October 1945, to August 1946, Caspari assessed theeffects of gamma rays on Drosophila sex-linked recessive lethality.
In Caspari's study the females were ﬁrst mated, placed on an egg
laying suppression diet, and then exposed to the gamma radiation(2.5 r/day) for 21 days with sperm stored in the female's spermatheca. In the Caspari study, there was an aging component tothe sperm that was not in the Spencer study. The dose rate used in
Caspari's study was much lower (13,200 times lower) than thatused in Spencer’s acute study at the same cumulative dose (Calabrese, 2011c).
The data from the chronic exposure study of Caspari supported
a threshold dose–response model. Stern initially rejected the1
In the case of the University of Rochester mammalian radiation geneticist
Donald Charles, despite the use of over 400,000 mice, his research was largely
unproductive, with no methodologically-based technical publications during thetime of the Manhattan Project which ended in 1946 (see Charles (1950) for a brief
descriptive paper). An additional summary paper (Charles et al., 1961) was published [after Charles's death (Anonymous, 1955a) that tried to salvage the research
effort with no obvious success. The failure of Charles to deliver a scientiﬁcallysigniﬁcant product for the Manhattan Project, given the level of resources directed
to it, represented a substantial failing.

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E.J. Calabrese / Environmental Research 142 (2015) 432–442

interpretation of Caspari as seen in written correspondence(American Philosophical Society, 1947a). Stern thought the ﬁndings were aberrant due to an unexpectedly high mutation rate of
the “controls” that obscured a linear dose response, yielding only
the appearance of a threshold response. Despite this rejection byhis mentor, Caspari dug into the published literature and foundconvincing support for his rather than Stern’s interpretation(Kaufmann, 1947; Muller, 1945, 1946b; Rajewsky and TimofeefRessovsky, 1939). To his credit, Stern accepted the data-based argument of Caspari.
Caspari's data were unexpected and somewhat troubling tohim because they challenged the linear paradigm of the radiation
genetics community. Therefore, Caspari decided to send his ﬁndings to another leading researcher, Milisav Demerec, head of genetics at Cold Spring Harbor, for review and comment. Caspari was
looking for a way around this problem (i.e., alternative interpretation) and hoping that the inﬂuential Demerec might offer asolution. Reﬂecting the bias of the radiation genetics researchcommunity at this time, Demerec wrote back to Caspari, acknowledging the problematic nature of the data, and rather thanhimself providing the hoped for insight, asked Caspari what could
be done to "save the hit theory" (American Philosophical Society,1947b). There was little question that the Caspari data had createda problem and, in fact, it would be referred to by Stern as a“problem” in future correspondence [Letter of Stern to Noviski –(American Philosophical Society, 1948). Demerec would later become a member of the BEAR I Committee, Genetics Panel thatrecommended the acceptance of the linear dose–response model.
While Stern seemed to accept Caspari's ﬁndings that supported
the validity of his control data, he nonetheless challenged theauthenticity of the data in other ways. The manuscript that Stern
and Caspari developed in the late summer/early fall of 1946 contained a six-page discussion, mostly arguing that Caspari's (rather
than Spencer's) ﬁndings should not be accepted until it could beshown why his threshold-supporting data differed from the earlier
linear dose–response ﬁndings of Spencer. This position, in and of
itself, was problematic in that the two papers had several dozen
important methodological differences (e.g., temperature of 18 °C
vs. 24 °C, egg-laying suppression vs. enhancement diets, irradiation by X-rays vs. gamma rays, young vs aged sperm, male vs female exposures and numerous other differences – [see Table 2,(Calabrese, 2011c), making it virtually impossible (if not impractical) to resolve the differences.
Even though the Caspari study adopted technical and methodological improvements over the Spencer study and had avoided
serious operational errors of the Spencer study (e.g., Spencer's
failure to control temperature, his combining of treatment groups
with the same cumulative exposure but with dose rates that differed by up to 2.5 fold, his failure to match control and treatmentgroups over the same time periods, and his inconsistent calibration of the X-ray machine, etc.) and errors in the modeling of low
dose responses (see detailed criticisms – (Bonnier and Lüning,
1949; Bonnier et al., 1949 ), it was strangely the Spencer study
with its linear dose response that became the gold standard andnot the Caspari study.
Discussion in the Caspari paper, as noted above, made it clearthat the ﬁndings in support of a threshold should not be accepted
until the differences between the two papers could be resolved. As
untenable as this position was, Stern's actions were even more
inexplicable as he would not place a similar constraint upon theﬂawed Spencer paper that supported linearity. It is bizarre, if notunheard of, for investigators to ask the scientiﬁc community not to
accept the validity of their ﬁndings until it could be reliably determined why their ﬁndings differed from a study of considerably
lesser quality and reliability. Moreover, not placing at least thesame constraints on the weaker study, for which Stern was also a

co-author, calls into question the investigator's non-biased andobjective approach to research. As a very accomplished scientist,
Stern should have known that resolving differences between these
two studies was not realistically possible.
Stern's unusual behavior makes sense when viewed as an attempt to blunt any challenge to the linear dose–response model(i.e., by demanding that the data of Caspari not be accepted). Stern
ensured the success of this strategy by sending the Spencer andCaspari manuscripts to his own journal, Genetics, and by fully
controlling their publication, including the Caspari discussion.
There is no evidence that he submitted either of the papers for an
independent peer review as the papers were submitted to thejournal on November 25, 1947, and published less than ﬁve weeks
later in January 1948 (Caspari and Stern, 1948; Spencer and Stern,1948).
At this point it was not clear whether Muller had seen the
Caspari data prior to his Nobel Prize Lecture on December 12,
1946. During the Lecture he disavowed any possibility that athreshold dose response could occur in the induction of mutations
by ionizing radiation. He demanded a switch to the linear dose–
response model, stating, "there is no escape from the conclusionthat there is no threshold" (Muller, 1946a). Not knowing whether
Muller had seen Caspari's data in support of a threshold modelprior to his Nobel Prize Lecture, several science historians withconsiderable knowledge of Muller and that era were then contacted. Yet, none of these attempts answered the question. Fortunately, substantial correspondence between Muller and Stern,
Caspari, Spencer and others was obtained from archival libraries.
The archived records revealed that Stern wrote to Muller on September 24, 1946, to request his services in reviewing the Casparimanuscript in preparation for journal submission. A follow-up
letter from Muller on September 27, 1946, accepted this invitationand on November 6, 1946, Stern sent the manuscript to Muller at
the University of Indiana. On November 12, 1946, Muller acknowledged receipt of both the letter and the manuscript. He also
indicated that he had brieﬂy read the manuscript and recognizedthat the ﬁndings supported a threshold dose response, seriously
challenging the linear model. Muller strongly encouraged Stern toﬁnd the means to undertake a replication study and indicated that
he would try to provide a detailed evaluation prior to his Nobel
Prize trip to Europe in early December. Clearly, this November 12th
letter acknowledged that Muller had seen Caspari's data, understood the challenge to the linearity model, was not dismissive of
the ﬁndings and acknowledged Caspari's competence and theneed to repeat the ﬁndings (see Table 1 for the series of Stern/
Muller correspondence statements).
Muller's evaluation of the Caspari manuscript occurred ﬁve
weeks after his Nobel Prize Lecture in the form of a detailed letterto Stern dated January 14, 1947 (American Philosophical Society,1947c). Based on this analysis, Muller had not changed his opinion.
He unequivocally stated that he could not ﬁnd any meaningful
criticism of Caspari's work (i.e., "I have so little to suggest in regard
to the manuscript.") and he restated the need to replicate theﬁndings (i.e., "Unfortunately, therefore a replication seems to be
imperative."). Thus, the statements written in private by Muller to
Stern were those of a scientist, while his unequivocal public rejection of the threshold model at the Nobel Prize Lecture was
deceptive and not without ideological underpinnings. Knowingthat uncertainty existed in the low dose zone and that further
study was needed, Muller could have acted more forthrightly by
pronouncing his conditional rather than categorical support of the
LNT model in Stockholm. Even four months later he remained
steadfast and continued to advocate his unqualiﬁed support for
the linear dose–response model. In a presentation to the New York
Academy of Medicine in 1947, he stated that “there is then absolutely no threshold dose…and even the most minute dose carries a

E.J. Calabrese / Environmental Research 142 (2015) 432–442

Table 1
Letter correspondence demonstrating that Muller had seen and considered Caspari's threshold supportive ﬁndings prior to his Nobel Prize lecture on December
12, 1946 (American Philosophical Society, 1946/1947; Calabrese, 2011c).
September 24, 1946 – Stern to Muller:“Dr. Caspari's report on his work is now being typed and I wonder whether we
could bother you with sending you a copy for your new comments.”
September 27, 1946 – Muller to Stern:“Also, I'd be glad to see Caspari's paper too.”November 6, 1946 – Stern to Muller:“Caspari's manuscript has ﬁnally been typed and we would appreciate verymuch your critical reading of it.”November 12, 1946 – Muller to Stern:“I have just arrived from an absence of over 2 weeks and ﬁnd the Casparimanuscript here waiting for me. Unfortunately, it catches me again when I
am in a tremendous pressure of work, trying to make up both the trip justpassed and for another one to come in a few weeks. However, I see that it isvery important and shall do all I can to go through it in a reasonable time,surely before I leave again early in December. I hope that Caspari can waitthat long if necessary. In the meantime I wonder whether you are having any
steps taken to have the question tested again, with variations in technique. It
is of such paramount importance, and the results seem so diametrically
opposed to those which you and the others have obtained, that I should thinkfunds would be fourth coming for a test of the matter. It is not, of course, that
I doubt Caspari's reliability at all, but only that I naturally share the same
doubts which he himself expressed. Of course, I am only judging by thesummary and a quick glance through the paper, and have not had the opportunity to read the details.”

deﬁnite chance of producing a change exactly proportional to thesize of the dose” (Muller, 1948).
Muller's statement in a letter to Stern (American PhilosophicalSociety, 1947c) about having “so little to suggest in regard to the[i.e., Caspari] manuscript” may not have been quite truthful, as
Muller himself was most likely responsible for the only twochanges introduced to the paper prior to its submission to thejournal Genetics. With the exception of these two changes, thepublished study in Genetics was identical in every way to that
paper which was sent to both Muller for his pre-submission review and to the Atomic Energy Commission (AEC) in 1947. In thejournal version, the ﬁrst and most signiﬁcant change was the deletion of a key sentence in the Conclusion of the 1947 AEC version(Caspari and Stern, 1947). The deleted sentence is as follows:"From the practical viewpoint, the results presented open up the
possibility that a tolerance dose for radiation may be found, as far
as the production of mutation is concerned" (page 15). This
statement indicated support for the threshold dose–responsemodel. The second change was signiﬁcant in that it added thename of Hermann J. Muller to the Acknowledgments of the published paper. It seems more than just coincidence that the only
two changes imparted to the journal version consisted of (1) the
deletion of a concluding statement in support of a threshold dose–
response model and (2) the simultaneous addition of Muller'sname to the acknowledgment section. There should be little doubtthat removing the threshold conclusion statement was of profound beneﬁt to Muller as it would help him sustain the ideological dominance of his favored LNT model. Muller clearly had themeans, motive and opportunity to mitigate the threat imposed by
Caspari's paper on the LNT model. So, was Muller responsible fordeleting the key concluding sentence in support of a thresholdmodel? Well, we may never know for sure, but strong circumstantial evidence seems to point in that direction.
In the aftermath of the Nobel Lecture, Stern followed Muller's
suggestion to repeat the ﬁndings of Caspari. However, his two
experienced doctoral researchers, Spencer and Caspari, had left for
the College of Wooster and Wesleyan University in Middleton,
Connecticut, respectively. Consequently, Stern tapped a new
Master's student, Delta Uphoff, a recent graduate of Russell Sage

435

College of Albany, New York, to replicate the Caspari research(Calabrese, 2011c). Data from her ﬁrst experiment piqued Sternbecause her control values for mutation rates were about 40%
below those found in the literature, including Caspari's study.
Stern expressed his concern to Muller and also asked Muller toshare his largely unpublished data with him on variation among
controls for the mutation rates of aging sperm in the fruit ﬂy. In aseries of letters between Muller and Stern, Muller conﬁrmed thatthe ﬁndings of Uphoff were not reliable and that the unpublished(and published) data were supportive of the Caspari control results. Muller's data led to an acknowledgment in the discussionsection of the Uphoff and Stern manuscript (Uphoff and Stern,1947) that the control group data were not interpretable and thatthe low control group value was most likely due to investigatorbias. Thus, in a rather unprecedented move, Stern was quick toplace blame on the inexperienced Uphoff. This manuscript, which
importantly acknowledged the assistance of Muller, was sent to
the Manhattan Project/AEC where it became classiﬁed and publicly unavailable. Thus, the acknowledgment by Stern of Uphoff's
unreliable control data, together with the letter exchanges between Muller and Stern regarding the reliability of Caspari's control data, clearly indicated that Muller had strong conﬁdence in
the Caspari and not the Uphoff control data (Calabrese, 2011b).
Stern then had Uphoff undertake a follow up replication study.
She again reported a similar unacceptably low control group response. As in the ﬁrst case, the ﬁndings were again not interpretable. Finally, in a third experiment that was undertaken, another problem arose. This time it was not the control group, which
seemed to respond as expected, but the treatment group whose
response far exceeded that predicted by a linear dose–responsemodel. At this point, Uphoff had ﬁnished her degree and eventually joined the National Institutes of Health (NIH) as a staff researcher. However, the damage was done to the Stern initiative
regarding the Manhattan Project/AEC. Each attempt to replicate
the Caspari ﬁndings had signiﬁcant problems. Could anything besalvaged?
In January of 1949, Stern decided to submit a technical note to
the journal Science, integrating the ﬁve major experiments conducted under his direction for the Manhattan Project/AEC. These
involved the studies of Spencer and Caspari and the three Uphoff
replications. In this Science paper, Stern attempted to rescue theﬁrst two Uphoff experiments that he already knew had aberrant
control groups (Uphoff and Stern, 1947) and, according to multiple
letter exchanges (Table 2), Muller also knew. Stern also chose toignore certain data that were not in support of the linear model(Caspari and Stern, 1947) and, again attacked the Caspari study as
aberrant even though nothing had changed except for the occurrence of even more data supporting the reliability of Caspari's
Table 2
Stern–Muller temporal letter exchange concerning the aged-stored sperm control
mutation rate [see (Calabrese, 2015a) – supplement for a more complete letter
exchange].
Curt Stern wrote a letter to Hermann J. Muller on January 22, 1947 (American
Philosophical Society, 1947d) informing him that “At the present time it looks
as if our new control data [probably the results of the ﬁrst three months of
the ﬁrst Uphoff experiment; note that her ﬁrst month's reading was anespecially low mutation rate of 0.005%] for aged sperm are considerably
below those of Caspari's.” He then asked Muller to “send me your ﬁgures onrate of sex-linked lethal in sperm aged several weeks, (most desirably, if you
have them, data on three weeks), in comparison to control data from nonaged sperm?”
On February 3, 1947 (Lilly Library, 1947) Muller answered by stating that “….
sperm of males which are about a week old and have been copulating freely[as in Caspari's experiment] during that period have only about 0.07 or 0.08
per cent of lethal. Thus the latter sperm, after three weeks, should containsomething like 0.28 per cent of lethal.”

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E.J. Calabrese / Environmental Research 142 (2015) 432–442

control group. These multiple ﬂip–ﬂops by Stern were befuddlingand surely required explanation, yet none were provided. The inferior Spencer study continued to receive strong support fromboth Stern and Muller even though, as noted above, it had verysigniﬁcant problems, none of which was noted by Muller in his
letters to Stern regarding the research of Spencer, September 13,
1946 (American Philosophical Society, 1946) and Caspari on January 14, 1947 (American Philosophical Society, 1947c).
The Science paper of Uphoff and Stern (1949) was beneﬁcial
both to the LNT model and to Muller himself as its chief advocate.
Stern was successful in artfully molding the interpretations ofexperimental data to ﬁt the LNT mantra. He achieved this goal
while the scientiﬁc community remained unaware that he andUphoff (with Muller's support) had acknowledged just a year
earlier that their own ﬁndings were not interpretable. Now, in theabsence of any new data, these same ﬁndings were not only acceptable but also argued in support of the LNT model. And Caspari,
who had successfully challenged Stern earlier, now remained silent as his ﬁndings in support of a threshold model were being
undercut in favor of Muller's LNT model. As for Muller, he musthave surely felt relief as he was spared the trouble of having to
defend his highly deceptive comments at the Nobel Prize Lecture.
Since the Science paper (Uphoff and Stern, 1949) was only a short
one-page note, consisting mostly of a single table, Stern andUphoff promised the science community a more detailed followup paper that would provide important methodological information and other relevant data. However, Stern and Uphoff never did
publish the promised follow-up study and there exists no evidence
that their colleagues in radiation genetics ever requested them todo so.
The strategy of Muller and Stern to deceive and obfuscate on
the nature of the dose response in the low dose zone was successful. This is evidenced by the fact that the Spencer and Stern
paper (Spencer and Stern, 1948) and the Science technical note by
Uphoff and Stern became the highly inﬂuential and commonly
cited papers. These “ﬂawed” papers provided the scientiﬁc foundations upon which the linear dose response model was justiﬁed
to the science community and, nearly a decade later, to the U.S.
Congress at hearings (Congressional Hearings of 1957) partiallyinspired by the NAS report of the BEAR Genetics Panel (Calabrese,2013a; Crow, 1957; Glass, 1957; Joint Committee on Atomic Energy,
1957; Muller, 1957). On the other hand, the technically superior
and more relevant paper by Caspari in support of a threshold interpretation received virtually no attention; it was, in essence,
unfairly but successfully marginalized. Various leaders in the ﬁeld
repeated false limitations of the Caspari study (Higgins, 1951; Jolly,
2004; Singleton, 1954) that were inspired by the deceptive comments of Stern and Muller e.g., (Muller, 1950b, 1954; Uphoff andStern, 1949). For example Singleton (1954) echoed that Caspari's
study could not be accepted because it had an aberrantly highcontrol group. Ironically, this was Stern's original challenge that
already had been so effectively rebutted by Caspari and Muller's
own data (see Table 2 for letter exchange between Stern andMuller).
After the Science paper, Muller published several papers that
repeatedly criticized Caspari's study as being too unreliable because of its high control group data. For example, in his 1950 article entitled “Some present problems in the genetic effects ofradiation” in the Journal of Cellular and Comparative Physiology,
Muller (1950a) provided an explicit characterization of the ﬁndings produced by Caspari and Stern (1948). Muller states on page
10 “A recent paper by Spencer and Stern….extends the principle(i.e., one-hit principle) down to total doses of 50 r and 25 r”. In thenext paragraph, he states: “It is true, in a parallel paper….Caspariand Stern have reported results somewhat deviating from theabove.” In footnote 1 on page 10 of the article cited above, Muller

adds “Uphoff and Stern have published a report of further work,with doses as low as 50 r, given an intensity as low as 0.0165 r per
minute. The results obtained are entirely in conformity with theone-hit principle. A consideration of these results, together withthe early work, leads to the conclusion that the deviation ﬁrst
referred to (the Caspari and Stern (1948) ﬁndings) was caused by avalue for spontaneous mutation rate that happened to be unusually high.” Although this repeatedly false criticism by Muller was
indeed highly disconcerting, other geneticists seemed too willing
and ready to accept it, more or less on ‘blind faith” and without
proper review and veriﬁcation. If they had chosen to follow thedata originating from Muller himself (Muller, 1945) and his own
graduate students (Byers, 1954; Byers and Muller, 1952) as well asothers (Graf, 1972; Rinehart, 1969) then perhaps the ﬁndings ofCaspari, and not of Uphoff, would have received public attention
and support. Thus, Muller continued to perpetuate a false viewthat was discredited by his own statements/data. Shamefully,
there is no evidence that anyone challenged Muller on thesecontradictions. Furthermore, Muller claimed that the research of
Delta Uphoff and Curt Stern was “entirely in conformity with theone-hit principle” (Timoféeff-Ressovsky et al., 1935). What Mullerneglected to state was that Uphoff's ﬁrst two experiments displayed an aberrantly low control group responses based on Muller's own extensive data involving some 200,000 fruit ﬂies (Muller,1946). A letter from Curt Stern to Ernst Caspari (fall 1947)(American Philosophical Society, 1947a) addressed the control
group issue. It states: “The radiation data continues to be puzzling.
Delta's difference between control and exper[imental group] appears to be due mainly to a much lower control group value thanyours. However, Muller informs me that this data give an aged
control value close to yours. Thus, my ﬁrst idea that your results
could be “explained away” by assuming that your control value
happened to be unusually high, seems unlikely. Rather does Delta's control appear too low”. Muller's false and self-contradictory
statements about Caspari's ﬁndings may be understood within thecontext of his ideological focus on establishing the LNT model forrisk assessment and in the preservation of his legacy – a legacy
that would have been severely tarnished if the deceptive remarks
he made during his Nobel Prize Lecture had been discovered.
A further example of Muller's duplicity in promoting the LNTconcept was his inaccurate characterization of the dose-rate usedin the Uphoff experiments (Uphoff and Stern, 1949), which was
0.00165 r/min, i.e., 50 r in 30,240 min or in 21 days) (Uphoff andStern, 1949). In his paper entitled “Radiation Damage to the Genetic Material” in the American Scientist, Muller (1950b) indicatedthat their research extended "the principle of proportionality ofmutation to doses down to doses of 50 r and 25 r and of less than
0.001 r/min with a time–intensity relation differing by over
400,000 times from that of our high intensity dose." By using theincorrect dose-rate of o0.001 r/min (instead of 0.00165 r/min)Muller (1950b) extended the linear extrapolation over 400,000fold, some 150,000-fold greater than what the correct dose-ratewould have predicted. Just as in the case of validating the Uphoff
control groups (discussed above), no one challenged Muller on thispoint. It is doubtful that Muller's actions was a simple editorialtypo as it involved two discrete changes, removing a 65 andadding a o sign. Furthermore, Muller (1950b) had correctly citedthe value as 0.00165 r/min in a previous paper.

4. The NAS BEAR I Committee Genetics Panel
The actions of Muller and Stern (cited above) were critical inpersuading the radiation genetics community to adopt the LNT
perspective, which was reinforced at multiple levels. By the early
1950s, according to Crow (1995), LNT had become the dominantE.J. Calabrese / Environmental Research 142 (2015) 432–442

view of this group, despite having little support elsewhere. Thistiming is important as it set the stage for the actions of the NAS
Genetics Panel on the Biological Effects of Atomic Radiation, whichissued its landmark report on June 12, 1956, and published its
technical report in the journal Science (Anonymous, 1956a) laterthat month.
Since the nature of the dose response in the low dose range
was a critical issue, it would be important to know how the Genetics Panel debated this issue, what the nature of the debate was,what votes were taken on the general dose response issues, and
who were the leading participants in the discussions. The Genetics
Panel formally met on November 20 and 21, 1955, at Princeton
University and on February 5 and 6, 1956, in Chicago. Transcripts
were obtained for both of these meetings. The Panel had a follow
up meeting March 1, 1956, with partial attendance and only ameeting summary (i.e., no transcript was taken). Intermeeting
communications among Panel members were encouraged via theexchange of working documents and draft materials. These communications were typically preserved in the historical record, andit was generally possible to obtain copies of papers and correspondences of the Panel members on BEAR I from their respective
institutional libraries. Although that which was archived varied
according to each person, an effort was made to obtain complete
sets of information on all Panel members. As a result, copious ﬁleson Panel members were obtained, enabling the reconstruction ofPanel activity to a high degree.
The transcripts of the Genetics Panel indicate that the members
debated neither the nature of the dose response at low doses, theexpectations of a linear or a threshold dose response nor any otherdosimetric issue. Dr. Tracy Sonneborn from the University of Indiana, a Panel member and colleague of Hermann Muller, wrote a
general guiding statement of principles for the Panel to follow; see(Calabrese, 2015a) – Supplementary material. The basic framework
consisted of four principles, i.e., that all doses of ionizing radiation
were (1) harmful, (2) irreversible, (3) cumulative, and (4) displayed a linear dose–response relationship. No member of the
Panel challenged these perspectives. In fact, at the Princeton
meeting of the Genetics Panel, Professor Alfred H. Sturtevant from
California Tech asserted his disdain for the medical profession thatstill adhered to an anachronistic belief in the threshold dose response model. Sturtevant stated that he had "no doubt about thecorrectness of the linear dose response" and that any effort tofurther document support for it would only be for the "propaganda value" needed to educate and convince the non-geneticists;see (National Academy of Sciences (NAS), 1955) – Transcription,
November 21, 1955.
The Panel's single-minded uniformity of belief regarding thenature of the low-dose response was profoundly signiﬁcant as it
tended not only to limit discussion and preclude debate but also toensure adoption of their preconceived notions. Due to this lack of
discussion and absence of debate, the Panel was challenged to
identify other activities that could productively ﬁll its meetingtimes. The Panel Chair, Dr. Warren Weaver of the Rockefeller
Foundation, forged ahead and challenged the 13 geneticists on the
17-member Panel to provide estimates of genetic damage to the
U.S. adult population given a speciﬁc exposure to the gonads. The
purpose of this exercise was to see how closely individual estimates of damage might converge among a blended mix of highlevel expert geneticists who had collective experiences studying
an array of diverse populations, including fruit ﬂies, bacteria,
paramecia, yeast, human populations and clinical patients, among
others. Weaver argued that a greater convergence (i.e., agreement)
among individual damage estimates would tend to yield a greater
conﬁdence by society in the Panel’s scientiﬁc conclusions and recommendations. Although one geneticist resigned from the Paneldue to overriding academic commitments, the remaining 12437

considered the challenge and the need to independently complete
the assignment within about one month following the meeting of
February 5–6, 1956. Of the 12 geneticists three (Tracy Sonneborn,
Clarence C. Little and James V. Neel) eventually decided that there
was too much uncertainty for the question to be quantitatively
addressed with any degree of accuracy or reliability and that any
population-based estimates would simply be misleading. For example, Neel stated that the scientiﬁc foundations needed to makesuch estimates of genetic damage were so uncertain that providingthem would be a violation of his obligation to society as a scientist;
see the April 6, 1956 letter from Neel to Weaver, cited in Jolly(2004). After the refusal of these three Panel members to participate in the exercise and provide estimates, the nine remaining
geneticists may have had similar misgivings, at least to some extent, but nonetheless provided quantitative estimates of genetic
damage within the prescribed time; see (Calabrese, 2015a) –Supplementary material.
When the Panel ﬁnally published its paper in Science, it indicated erroneously that six (instead of nine) geneticists took up
the challenge and provided such estimates (i.e., "Six of the geneticists on this committee considered the ....problem."). This apparent discrepancy triggered a more extensive assessment ofcommunications among panel members and related information
regarding the estimates of damage. Chairman Weaver gave James
Crow the task of organizing the submitted material and integrating tables listing the damage estimates of each participating geneticist. As a result of this process, it quickly emerged that there
was considerable disagreement among Panel members concerning
the identity and appropriate use of methods and assumptions in
conducting the assignment. Thus, as one can imagine, confusion
about the assignment and the lack of a clear protocol yielded estimates of extreme variability. Panel members were highly uncertain of their own estimates, which often radically disagreed
with the estimates of fellow Panel members. In spite of the factthat each geneticist employed the linear dose–response assumption, the results of this exercise led to anything but a convergence.
A close reading of all the contributions reveals that some of the"experts" had little idea how to approach the problem. This can behighlighted in the case of James Crow, the last surviving memberof the Panel, who died in 2012. For example, on March 29, 1956,
Crow stated (Crow, 1956): "I shall use as a minimum estimate a
direct extrapolation from Drosophila and as a maximum some
calculation from the sex-ratio in the Japanese cities. An estimate
from mouse data turns out to be just about half way between
these, so I shall use it as the most probably estimate." The nonsequiturs inherent in such biological reasoning demonstrate how
poorly some of the leading experts addressed this issue. As theother geneticists expressed similar levels of uncertainty and disagreement, it is not surprising then that the Panel would share
their documentation with neither external reviewers nor the interested public.
A major problem arose as a result of the extreme variability
among the individual estimates. That is, the uncertainty of theseestimates would erode public conﬁdence in the Panel's pronouncements. Crow perceived the problem and memorialized hisconcern in a letter to Chairman Weaver of March 29, 1956: "Thelimits presented on our estimates of genetic damage are so widethat the reader will, I believe, not have any conﬁdence in them atall." Thus, Crow believed that if the Panel shared its uncertainty
with the public then the likelihood of winning their acceptance ofany scientiﬁc and policy guidance would be seriously threatened.
Crow then made a unilateral decision to exclude the estimates ofthree of the geneticists (i.e., Kaufmann, Wright and Demerec), thethree with the lowest estimated damage values; see (Calabrese,2015a) – Supplementary material for a detailed assessment foreach of these three excluded values. Although Crow’s decision

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E.J. Calabrese / Environmental Research 142 (2015) 432–442

markedly reduced the amount of variation within the group, thisinitial "adjustment" was simply not enough to solve the variability
problem. Crow then strongly urged the Panel not to share the six
remaining and highly variable assessments with the scientiﬁccommunity and public. The Panel eventually voted on Crow's recommendation, and the majority decided in favor of it, thus essentially eliminating anyone from the interested public or thescience community from critically examining the data or theprocess by which these estimates were derived. While a copy ofthe voting tally was obtained, speciﬁc information on votes ofindividual members was discovered for four members. Based on
their preserved correspondence, (Calabrese, 2015a) – Supplementary material, Crow, Glass, Muller and Sonneborn all voted not
to share the data.
The aforementioned analysis reveals that the Genetics Paneldeliberately falsiﬁed the research record in the Science article byreporting that only six geneticists provided estimates of radiationinduced genetic damage. This was patently false as nine geneticists
provided detailed estimates within the prescribed period of time.
There was no expectation and no established protocol for the exclusion of estimates as each geneticist on the Panel was considered
an independent world-class expert in his own area of genetics. The
person who excluded the three estimates was Crow, who lacked
the authority to do so. In fact, the exercise on estimating risk ofgenetic damage was designed to develop a gage of expert agreement or lack thereof. Removing the three estimates was a deliberate act to obscure and mitigate the magnitude of disagreement
and uncertainty that existed among the experts. Furthermore, thereport did not even acknowledge that three other Panelists refused
to participate in the exercise because too much uncertainty precluded the possibility of making any reliable estimates, (Calabrese,2015a) – Supplementary material. Finally, the Science article contained an inaccurate estimate of response variability in the rangeof plus or minus ten-fold on either side of the mean. More speciﬁcally, the Science paper states, "These six geneticists concluded,
moreover, that the uncertainty in their estimation of the mostprobable value was about a factor of 10. That is to say, theirminimum estimates were about 1/10, and their maximum estimates about 10 times the most probable estimate”. This 100-folduncertainty markedly misrepresented the range of uncertainty ofthe six remaining Panel geneticists for estimating the next generation, which had a mean uncertainty value of 756 (312.5 median). See Table 1 of identiﬁed individual values in Calabrese(2015a) – Supplementary material.
The Genetics Panel of the NAS, as a group, therefore deliberately sought to misrepresent the research record in their landmark
Science publication on three distinct aspects. These included: theincorrect statement that only six geneticists provided genetic damage estimates when nine did; the failure to report that threeother geneticists refused to provide any estimates at all because of
the high level of uncertainty of this exercise; and, ﬁnally, the uncertainty range for the six geneticists was given as 100 fold whenthe mean value was actually 756 fold. These actions of fabricationand falsiﬁcation by the Genetics Panel were undertaken to ensurethat governmental agencies, legislative bodies and the generalpublic would be more likely to accept the Panel’s LNT-derived
policy recommendations for assessing the risk of ionizing
radiation.

5. BEAR I Genetics Panel report – fallout
Following its acts of falsiﬁcation and fabrication of the researchrecord, the Genetics Panel continued to show its arrogance in theaftermath of the BEAR I Panel and at the start of BEAR II (fall,1956). In this case, several leading biologists had requested that

the Genetics Panel provide documentation that would explain/support its decision to recommend the adoption of the linear
dose–response model for risk assessment purposes, (Calabrese,2015b) – Supplementary material and Glass (1956). The biologists
noted that the BEAR I Panel had proclaimed the correctness of the
LNT model, but it failed to provide any written scientiﬁc basis for
its decision. Since providing documentation to support major decisions is the main mission of any NAS Committee, the BEAR I
Genetics Panel, by this standard, clearly failed to perform its
mission. However, in a decision that may be difﬁcult to understand, the Panel actually refused to do so, deciding instead to redirect its efforts to identifying research areas for future funding.
Furthermore, it is highly unusual, if not astonishing, that the Panelactually informed the President of the NAS, Detlev Bronk that it
had decided not to provide documentation to support the LNT
recommendation. In fact, no documentation in support of the LNTdecision ever existed at the time of the BEAR I Genetics Panelreport on June 12, 1956, and now it would have to be written wellafter the fact – a serious problem in and of itself. Secondly, thePanel members openly noted that they preferred to spend theirtime identifying research priorities for funding opportunities,some of which would be of interest to their own research laboratories. No evidence has been found to suggest that President
Bronk ever objected to the Panel’s no documentation decision,
which was shared with him in a letter from George Beadle, Chairof the BEAR II, Genetics Panel (Beadle, 1957) on September 11,
1957. Thus, the President of the NAS was complicit in the decision
not to require the BEAR Genetics Panel to document its support of
the LNT model.
The BEAR I and II Panels consisted of essentially the same individuals except for two changes. The Chair (i.e., Warren Weaver)
stepped down so he could award grants from the Rockefeller
Foundation to Panel members without an obvious conﬂict of interest, and one new person (TG Dobzhansky) who had been invited for BEAR I, but was unavailable at the time.
The BEAR I, Genetics Panel released their report amongst aﬂurry of media attention with front page stories in the New YorkTimes (Leviero, 1956) and Washington Post (Haseltine, 1956). Other
leading venues, including US New and World Report (Anonymous,
1956b), The Saturday Review (Muller, 1956), Time Magazine(Anonymous, 1956c, 1956a), Science journal (Anonymous, 1956c),
The Lancet (Anonymous, 1956f, 1956g) and others, also had articles
on the BEAR I Genetics Panel report. The New York Times called it
the most extensive study ever conducted by such a leading groupof experts. Yet, in retrospect the evidence shows that the effort
failed in critical ways, especially in not even debating the key
question concerning the nature of the low dose zone in the dose–
response paradigm. The Panel proclaimed the validity of the linear
model at the start and never felt the need to justify this fundamental decision, even following a subsequent challenge by leading
biologists. Such inappropriate actions of the Panel continued, as it
even deemed it necessary to fabricate and falsify the record intheir key Science publication to ensure that their views would be
accepted. All this was clearly expressed in newly unearthed records of the Panel’s correspondence. The dishonesty of the Panelwas nothing new as it was simply carrying on a tradition seeded a
decade earlier by Hermann J. Muller at his Nobel Prize Lecture.
The explicit deceptions of some Panel members continued evensome 35 years after the fact. For example, Panel member and geneticist Bentley Glass (Glass, 1991), in a book review about theRockefeller Foundation, retold the BEAR I, Genetics Panel story
reported in the 1956 Science article concerning how the Panelobtained its estimates of genetic damage in the U.S. population.
Glass wrote that Chairman Weaver sought to overcome vast disagreements among Panelists by instructing them to return to theirhotel rooms and work out their damage calculations individually.

E.J. Calabrese / Environmental Research 142 (2015) 432–442

The following day, Glass reports, the disagreements were profoundly diminished and a strong consensus emerged. The story by
Glass may well be how he remembered the event but his memoryis strongly contradicted by the factual record. The fabrications ofGlass started with his "authoritative" quote from Weaver that inspired the geneticists to return to their rooms. The quote does notexist in the meeting transcripts. The story of Weaver sending Panelists to their hotel rooms to work on their estimates and of theirreturning the next day in triumphal consensus likewise neveroccurred. In fact, Weaver charged them to return to their respective homes and gave them about a month to work on theestimates. Thus, once again, based on the transcripts and substantial subsequent written communications, Glass bears false
witness. Glass's most signiﬁcant fabrication is that the Panelists
actually reached a strong quantitative agreement. The consensus
story was not real but faked by Weaver and the Panel as discussed
above and detailed elsewhere, (Calabrese, 2015a) – Supplementarymaterial.
The highly regarded Glass, among whose honors included
being a President of the AAAS and Phi Beta Kappa, amongst numerous other honors, repeated, therefore, the long establishedfalse narrative, reinforcing the LNT mantra well into the modern
era of risk assessment and doing so with great appeal to his authority. This is therefore the story of not only how the U.S. andworld governments came to adopt the linear dose response forrisk assessment but also how its origins were forged by deception,
artful dodges and blind faith to become established, preserved,
protected and reinforced by those very people (e.g. Genetics Panelists) and organizations (e.g. NAS) that society is supposed totrust.

6. The Rockefeller Foundation and the LNTIn 1954, the Board of Trustees of the Rockefeller Foundation(RF) developed the proposition that it was necessary for the United States (U.S.) to undertake a major assessment of ionizing radiation on humans and the environment. One of their Board
members was Dr. Detlev Bronk, who was also serving at that timeas the President of the Rockefeller Institute for Medical Research(which would become Rockefeller University in 1965) and President of the U.S. National Academy of Sciences (NAS). Prior to thistime, Dr. Bronk had also been the President of Johns Hopkins
University and the President of the American Association for the
Advancement of Science (AAAS) in 1952. Bronk took the proposalof the RF Board of Trustees to the NAS and received permission toundertake this project as an ofﬁcial NAS activity (Hamblin, 2007).
This new project was called the NAS Biological Effects of Atomic
Radiation (BEAR) Committee. The project involved six independent technical panels for different areas of concern (e.g.,
genetics, pathology, oceanography and ﬁsheries, agriculture, meteorology, and waste disposal and dispersal). The panels werecreated by Dr. Bronk and administratively overseen by the RF.
All six BEAR Committee expert panels were chaired by renowned experts in their respective ﬁelds except for the Genetics
Panel, which was chaired by Warren Weaver, a mathematician andlong-time administrator at the RF (Rees, 1987). Interestingly, Bronk
selected Weaver to chair the Genetics Panel and, as such, this selection represented a striking deviation in panel construction andleadership. Although multiple individuals with considerable relevant scientiﬁc expertise and strong leadership skills were already on the Genetics Panel, none of them would be selected as
Chair. Overlooked in the selection process were: George Beadle,
the future President of the University of Chicago (and 1958 Nobel
Prize winner); Alexander Hollender, the highly regarded scientiﬁc
administrator at Oak Ridge; Clarence C. Little, the past President of439

the Universities of Maine and Michigan; and Milislav Demerec,
Head of Genetics at Cold Spring Harbor.
In the selection of panel members, one suspects that Bronk andWeaver may have intended to “stack the deck” with radiation
geneticists who supported the LNT. For example, Ralph Singleton
was a radiation geneticist at the Brookhaven National Laboratory
who at the time, questioned the linearity hypothesis and reported
a non-linear relationship between mutation rate and dose rate,with disproportional increases at higher doses (Singleton, 1954;
Richter and Singleton, 1955; Sparrow and Singleton, 1953). In an
April 17, 1955 article in the New York Times, (Anonymous, 1955b)
Singleton challenged the linearity concept for genetic damage
stating “there probably is a safe level of radiation, below which no
genetic changes occur.” Singleton’s expertise and the timing andtopic of his publications would seem to have easily qualiﬁed him
for membership on the Genetics Panel, assuming of course that the
key objective was to form a panel representing diverse viewpoints
to encourage discussion and thoughtful consideration. As it turns
out, Singleton was not appointed to the Genetics Panel but to theAgriculture Panel of BEAR I.
The BEAR Panels were the creation of the RF, fully funded by
the RF, administered by RF staff and directed by a member of the
RF Board of Trustees, who was also President of the NAS. Not only
did Dr. Bronk help to conceptualize the project, but he was alsopart of the organization that funded the project and led the organization that received the funding and oversaw the project, including guiding the selection of panel chairs and their members.
For a long time, the RF was a major funding organization forradiation geneticists, including members of the Genetics Panel. The funding of such members extended over three decades,much of which was during the employment of Weaver and also
under his direction. As noted in Wynchank (2011) and prior to thecreation of the Genetics Panel, the RF had funded nearly four
million dollars to the University of Indiana for research in the areaof radiation genetics alone. Such funding supported the research
activities of Professors Sonneborn and Muller, both members of
the BEAR Genetics Panel.
Weaver was clearly aware of the importance of RF funding toradiation geneticists and showed no reluctance in connecting thePanel’s success to opportunities of lavish funding for its members.
Weaver speciﬁcally stated at the February 5, 1956 meeting of the
Genetics Panel that he would "try to get a very substantial amountof free support for genetics if at the end of this thing we have a realcase for it. I am not talking about a few thousand dollars, gentlemen. I am talking about a substantial amount of ﬂexible and free
support to geneticists”, (National Academy of Sciences (NAS)/National Research Council (NRC), 1956) – NAS transcripts, February 5,
page 35. As part of his interaction with the Genetics Panel, he
prefaced his funding remarks with the statement that "There may
be some very practical results – and here is the dangerous remark– don't misunderstand me. We are just all conspirators here together." The remarks of Weaver were blunt and remarkably focused linking the project outcome to the funding interests of thegeneticists on the Panel. Such a blatant coupling of funds andoutcome were highly manipulative.
Could such an inducement, as grant support, really be persuasive enough to affect the performance, judgment or integrity ofesteemed scientists on an NAS Panel? In his 2007 dissertation(Seltzer, 2007), Seltzer sheds some light on this question. He
concluded that members of the Genetics Panel saw themselves asfunding advocates for radiation genetics (p. 285 footnote 208).
Furthermore, it was hoped that the Genetics Panel, which would
continue into the foreseeable future, would affect the directions
and priorities of funded research in genetics. Seltzer (2007) also
further showed that such expectations were in fact evidenced incorrespondence between members of the Genetics Panel, i.e.,

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Beadle, Dobzhansky, Muller and Demerec. In a letter to Beadle,
Demerec (American Philosophical Society, 1957a) offered a funding plan that could be achieved by “setting aside a fund (let us say,one hundred million dollars), to be administered by some competent organization (such as the National Academy of Sciences)and used during a period of 20 or 25 years to fund already functioning research centers so as to attract and train ﬁrst rate scientists”. Dobzhansky (American Philosophical Society, 1957b) responded to this proposal by stating that he would “needless to say,be all in favor (of) $100,000,000 for research in general genetics….
but I would ﬁnd it hard to keep a straight face arguing that they(general genetics) must be studied to evaluate the genetic effectsof radiation on human populations”. This evoked from Demerec(American Philosophical Society, 1957c) the statement that “I,
myself, have a hard time keeping a straight face when the talk is
about genetic deaths and the tremendous dangers of irradiation. I
know that a number of very prominent geneticists, and people
whose opinions you value highly, agree with me”. Finally, Dobzhansky (American Philosophical Society, 1957d) responded bysaying “Let us be honest with ourselves – we are both interested in
genetics research, and for the sake of it, we are willing to stretch apoint when necessary. But let us not stretch it to the breaking
point! Overstatements are sometimes dangerous since they resultin their opposites when they approach the levels of absurdity.
Now, the business of genetic effects of atomic energy has produced
a public scare, and a consequent interest in and recognition of(the) importance of genetics. This is to the good, since it will makesome people read up on genetics who would not have done sootherwise, and it can lead to the powers-that-be giving money for
genetic research which they would not give otherwise” (American
Philosophical Society, 1957d).
These shared comments by key members of the Genetics Panelprovide previously unknown insights into motivations of theleading radiation geneticists of that era and the group that legitimized LNT for use by society. According to Seltzer (2007), theseletters made two points: (1) that the geneticists were quite focused on the viability of their discipline and (2) that they werecognizant of and acted upon opportunities to manipulate thecurrent situation (e.g., to stretch a point) for the purpose of increasing the likelihood of greater funding. It seems as though thepersuasiveness of grant funding is more powerful than one could
have imagined, even for esteemed scientists.
When viewed from a grander perspective, the RF displayed anundue and unheard of inﬂuence over the course of cancer risk
assessment within the United States and throughout the world.
The RF directed and funded the entire process that resulted in the
adoption of the LNT, all hidden within the prestige of the U.S. NAS
due to the multiplicity of roles played by Bronk. Weaver used his
long-honed knowledge and skills concerning the vulnerability ofacademics for external grant funding and lured Panel memberswith funding possibilities on the basis that their area would beseen as important to society. Such manipulations raise serious
ethical issues. In fact they paved the way for the very activities that
occurred within the Genetics Panel, that is, misrepresenting the
research record to enhance its policy recommendations. To ensure
a “proper” narrative, Weaver the mathematician, and not one of
the geneticists, drafted the ﬁnal report of the Genetics Panel(Glass, 1991). At an organizational level, the RF manifested hegemony over the BEAR Genetics Panel, warping and corrupting a risk
assessment process that had lasting, social and economic public
policy consequences. At an individual level, Bronk’s failure to require the panel to document the scientiﬁc basis for the LNT recommendation and the Panel members’ self-serving decision to
identify funding opportunities instead of writing the report, together represent unscrupulous behaviors that enabled them toestablish the legitimacy of the LNT model without having to

defend their position and, at the same time, optimizing their future funding options.

7. Conclusions" The recommendation by the U.S. NAS in 1956 to adopt the LNTmodel was rapidly accepted by governments worldwide andprovided the basis for estimating cancer risks from ionizing
radiation and chemical carcinogens over the past six decades.
" The recommendations of the U.S. NAS BEAR I Committee, Genetics Panel were ideologically-driven with no written scientiﬁcbasis provided by the Panel.The Genetics Panel explicitly refused
to provide a written documentation when formally challenged
to explain their recommendations. Moreover, the President of
the NAS became complicit in the Panel's questionable and irregular actions by taking no corrective action, even after receiving notiﬁcation by letter of the Panel's refusal to provide
such a report.
" Studies under the direction of Curt Stern at the University ofRochester/University of California-Berkley using Drosophila
provided the scientiﬁc basis for the LNT of the BEAR I Genetics
Panel. Detailed re-analyses of these studies has revealed serious
ﬂaws in the acute study by Warren Spencer and in key follow up
chronic exposure experiments by Delta Uphoff. Curt Stern intentionally concealed critical limitations of the Uphoff ﬁndings
which had Stern and Uphoff characterize these ﬁndings as“uninterpretable”. Stern, in cooperation with Hermann Muller,
deliberately misrepresented and marginalized the ﬁndings ofErnst Caspari which supported a threshold model.
" The NAS Genetics Panel committed scientiﬁc misconduct byfalsifying, fabricating and then publishing in the journal Scienceits doctored estimates of human genetic risk to radiation exposures. The Panel's deceits were designed to prevent the scientiﬁc community and the general public from knowing the
profound uncertainties entailed in its genetic risk estimates,
thereby insuring the ready acceptance of its policy
recommendations.
" Current cancer risk assessment policy and practices are based on
fraud and deception by key leaders of the radiation geneticist
community and by the U.S. NAS, BEAR I, Genetics Panel. Their
deceptions were uncritically adopted by regulatory agencies andthe scientiﬁc community worldwide and provide the foundationof cancer risk assessment and risk communication messages.
The implications of such fraudulent actions are profound andlikely to affect: human health risk assessment, adoption and useof new technologies, cost beneﬁt assessments at multiple societal levels, toxic tort actions/decisions, and in the education of
the public on vast areas of environmental health and medical
treatment practices.

Funding sources
Research activities in the area of dose response have been
funded by the United States Air Force and ExxonMobil Foundation
over a number of years. However, such funding support has notbeen used for the present manuscript.

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