Molecular and Cellular Biology, December 2001, p. 8238-8246, Vol. 21, No. 23
New Ways of Initiating Translation in Eukaryotes?
This letter to the editor is a response by a large number of
investigators in the field of protein synthesis to the minireview published by Dr. Kozak in Molecular and Cellular Biology
(9). This minireview attempts to create significant doubts
regarding the published literature that we believe are unwarranted and
to bolster Dr. Kozak's own point of view regarding translation
initiation. We therefore take serious issue with the scholarliness of
the Kozak minireview. As will be shown, the Kozak minireview contains numerous distortions of fact and of published data and selectively utilizes the published literature. In every field of research there are
legitimate concerns regarding the interpretation of results and the
reproducibility of certain published data. Several of the issues raised
by Dr. Kozak are legitimate in this regard, but they are not new and
have hardly gone unnoticed, having been raised in scholarly and
critical reviews elsewhere. At issue here is not the right to
critically question results and interpretations but rather whether the
Kozak minireview is scholarly and its tone is professional.
We point out that much of the work challenged in the Kozak minireview
was published in Molecular and Cellular Biology, as well as
other leading peer-reviewed journals, and forms a mainstream of
research on protein synthesis which is taking place in scores of
laboratories around the world. In this minireview, Dr. Kozak dismisses
three novel mechanisms for translation initiation which have now been
well studied and extensively documented. One mechanism is internal
ribosome entry, which she rejects in favor of ribosome scanning, a
mechanism for translation initiation which she proposed over 20 years
ago. In ribosome scanning, it is proposed that the 40S small ribosome
subunit enters the mRNA from the 5' cap and undergoes a linear 5'-to-3'
search for the initiation codon, which is typically an AUG. Internal
ribosome entry involves the internal association of ribosome subunits
at or near the initiation codon without the need for entry from the 5'
end of the mRNA. A second mechanism opposed by Dr. Kozak is the
initiation of protein synthesis without Met-tRNA, a universal and key
component, as shown for several insect virus mRNAs. The ability to
carry out translation without this initiator tRNA, and from the A site
of the ribosome, has enormous implications for our understanding of
protein synthesis and its evolution. A third mechanism of translation
initiation which Dr. Kozak takes issue with is known as ribosome
shunting or discontinuous scanning, which combines features of 5' entry of ribosomes by scanning and the internal translocation of ribosome subunits without further scanning to the initiation codon. It is clear
to a great many researchers, as represented by the signatory list
below, that the initiation of protein synthesis in eukaryotes is
dynamic and flexible, involving a variety of mechanisms that have
evolved to meet the complex demands of eukaryotic cells and viruses.
Dr. Kozak has spent more than 10 years in strenuous opposition to the
evidence for viral internal ribosome entry and the recognition of
specific viral cis-acting internal ribosome entry site
(IRES) elements. The minireview now attempts to use almost entirely the same kinds of arguments against cellular IRESs and other means of
nonscanning translation initiation that Dr. Kozak used previously in
her unsuccessful efforts to disprove viral IRESs. Whether Dr. Kozak
explicitly acknowledges internal ribosome entry as an established fact,
at least for viruses, is not at all clear in the minireview, although
she does compare translation functions to the encephalomyocarditis virus (EMCV) IRES, but without comment or acceptance. It would be
fairer to the reader and more intellectually honest to explicitly acknowledge internal ribosome entry as an established fact, at least
for viruses, or It is not practical to document here all of the examples in which
published results were inappropriately presented in the minireview by
Dr. Kozak. We refer readers to a recent comprehensive review which
summarizes the current evidence in support of viral and cellular IRES
elements and alternate mechanisms of translation initiation in
eukaryotes and briefly overviews some of the key techniques which were
questioned by Dr. Kozak (7). Consequently, we list below
just several specific examples which are emblematic of the serious
issues which are of concern to us.
Several reasons are described by Dr. Kozak for dismissing reports of
cellular IRESs. Dr. Kozak argues that because cellular IRESs often
represent modest translation increases over background levels, they
result from fortuitous positioning of RNA sequences in experimental
constructs. This argument ignores the evidence that IRESs have been
shown to represent a range of activities from weak to strong and to
function by a variety of mechanisms. Indeed, the expression of many
cellular genes encoding regulatory proteins is often tightly controlled
at multiple steps to guarantee that correct protein levels are
achieved, which is not generally equivalent to high protein levels. An
IRES may therefore be relatively weak, but in combination with other
levels of gene control, it achieves significant or correct protein
expression levels under different physiological conditions. One
example is the IRES of the proto-oncogene c-sis, which
encodes platelet-derived growth factor 2 (PDGF2). This IRES is
activated severalfold during megakaryocyte differentiation, in
conjunction with induction of PDGF2/c-sis gene expression during
differentiation (1, 16). The modest translation
stimulation directed by the cellular PDGF2 IRES fine tunes PDGF2/c-sis
gene expression during differentiation. Similar mechanisms are
likely employed by other critical regulatory genes and may have
widespread implications for cellular growth and development. Thus, it
is arbitrary to dismiss cellular IRES elements as physiologically irrelevant artifacts merely because their effects on translation are
moderate. A more considered view is that regulatory elements act at all
levels of gene control, including transcription, mRNA transport,
and mRNA stability and translation, and permit exquisite control
precisely because they involve multiple and modest additive effects
which can be independently combined and regulated.
There are several functional ways to study IRESs. Construction of a
dicistronic mRNA containing an internal downstream second open reading
frame that is ordinarily not translated is typically used to detect
IRES activity. Other approaches include insertion of very stable,
translation-blocking hairpin structures upstream of the IRES and
biochemical detection of IRES interaction with initiation factors and
ribosome subunits. Important control studies must be performed to
validate the integrity of the dicistronic mRNA and to exclude the
presence of cryptic promoters or aberrant splicing that could lead to
production of subgenomic mRNAs or removal of intervening RNA sequences
that would normally prevent internal translation initiation by ribosome
scanning. With this in mind, apart from one "potential" cellular
IRES, Dr. Kozak dismisses all other published reports as artifacts
arising from improper experimental methodologies, a lack of proper
control studies, or poor experimental design. However, most but not all
cellular IRES studies included the use of other RNA segments that did
not contain IRES elements or IRES sequences with defined mutations, which failed to mediate internal ribosome initiation. Thus, selective translation by internal ribosome entry was in fact shown to be specific
for a small number of RNA elements. These controls were largely ignored
in the Kozak minireview, inappropriately casting doubt on the integrity
of the conclusions from these reports. Dr. Kozak is particularly
critical of cellular IRES reports because the background control level
of translation in the absence of the IRES varies between different
constructs and because it is not zero. This argument can be misapplied
to most molecular systems. For instance, deletion of all transcription
elements seldom completely abolishes activity, and the basal activities
of different control constructs typically vary. As proof for this view,
Dr. Kozak points out that an antisense version of a putative cellular
IRES directed translation at 40% of the level of the sense form
(13). However, in other examples the antisense
verification did not function as an IRES. In other cases, Dr. Kozak
asserts (in the absence of any evidence to support her view) that a
control RNA sequence has depressed translation, making it only appear
that the cellular IRES element directs translation initiation. As one
example, the Kozak minireview inappropriately compares experiments
described in two papers (11, 21). In the Nature
paper (11), the BiP IRES mediated translation of the
second cistron 15-fold over the Antp control sequences. Importantly,
introduction of a hairpin at the 5' end of the dicistronic mRNA
completely abolished translation of the second cistron (Fig. 2 in
reference 11), demonstrating that the BiP sequence
has IRES activity. In the Nucleic Acids Research paper
(21), the BiP IRES was stimulated 10-fold over the Antp
sequence; as Dr. Kozak pointed out, translation was lower (2.5-fold)
compared to the "empty" vector control. This was interpreted by the
authors as readthrough mediated by the 30-nucleotide sequence located
between the two cistrons. This does not constitute a serious "discrepancy of results," in contrast to its presentation by Dr. Kozak. In addition, while studies have shown that varying the length of
the intercistronic region influences translation initiation frequency
(5), a potential confounding problem, the effect acts
predominantly on scanning-dependent rather than internal initiation of translation.
Dr. Kozak asserts that cryptic promoters or cryptic splicing of RNAs
cannot be excluded as a source of smaller mRNAs that could be
translated from truncated positions, providing the false impression of
internal ribosome initiation or initiation by ribosome shunting. Dr.
Kozak is not alone in expressing concern regarding some claims for
internal ribosome entry, particularly when there is no accompanying
data verifying the integrity or size of the mRNA species. Indeed, a few
studies noted unanticipated smaller transcripts and noted that they
likely arose from splicing, generally at low levels, from a few of the
dicistronic constructs (e.g., see reference 6).
However, this study demonstrated that the translation of the second
cistron could not have occurred from the low-abundance monocistronic
mRNA. Dr. Kozak cites the fact that unanticipated splicing was
sometimes detected but does not present the data fully and accurately.
Additionally, many studies involved in vitro-synthesized mRNAs that
were monitored in cell-free systems or examined after expression in
cultured cells, and the RNAs were found to be intact. While Dr. Kozak
highlighted instances in which important RNA structural data were
absent, she often failed to reference studies in which it was included
and the RNAs were found to be intact. In some other cases she
inappropriately dismisses the data as of poor quality or not
sufficiently sensitive. For example, Dr. Kozak criticized published
work on the vascular endothelial growth factor (VEGF) IRES as not
convincing because of the presence of an internal promoter but failed
to cite another paper which showed that translation initiation from an
internal promoter cannot account for VEGF translation results
(8). Again, it is not appropriate to assume that moderate
translation effects, which can be quite important biologically, are
artifacts because they do not conform to an arbitrary value. Internal
initiation of c-Myc2 protein synthesis was similarly dismissed by Dr.
Kozak despite evidence for only a single mRNA because transfection of the mRNA itself into cells, compared to its expression from a DNA
vector, failed to lead to translation (17, 18). It was suggested by the authors of these two papers that the c-myc
IRES might require nuclear binding proteins to function, which is
reasonable given the importance of noncanonical factors for the
activity of certain viral IRESs (7). This was rejected by
Dr. Kozak, and other well-controlled studies which demonstrated c-Myc
IRES function were not cited (e.g., reference 12).
Thus, the minireview provides the false impression that only limited
and poorly controlled research has been performed on cellular IRESs.
Dr. Kozak also asserts that biochemical studies have never been
conducted to show that initiation factor 4G (eIF4G), a key factor that
promotes ribosome binding, can associate with sufficient affinity to a
natural IRES so as to mediate internal ribosome entry. This conclusion
is meant to cast doubt on the validity of translation by internal
ribosome entry in eukaryotic cells. In fact, Lomakin, Hellen, and
Pestova (10) directly measured the affinity of the central
domain of eIF4G alone and as a complex with eIF4A for the EMCV IRES and
for Dr. Kozak questioned the quality and integrity of work which
demonstrated the possibility of initiator-independent translation from
the ribosome A site, as shown to occur in the cricket paralysis virus
(CrPV) mRNA (19). This is a recent seminal finding in the
field of protein synthesis. Importantly, a landmark paper (15), which demonstrated that a related insect virus IRES
is also translated without tRNA A number of studies have identified yet another alternate mechanism for
translation initiation known as ribosome shunting. As it occurs in
adenovirus mRNAs expressed during the late stage of infection, ribosome
shunting was shown to involve sequences in the viral 5' noncoding
region that are complementary to 18S rRNA (22). Dr.
Kozak's minireview misrepresents the central conclusion of this paper,
falsely stating that this study claims to have demonstrated direct
interaction between mRNA and 18S rRNA for initiation of translation by
ribosome shunting. In fact, this study concluded that ribosome shunting
on adenovirus late mRNAs might occur by any of several mechanisms that
involve sequences complementary to 18S rRNA, including but not limited
to structural RNA mimicry or direct interaction with 18S rRNA. Dr.
Kozak also asserts that only rudimentary mapping, large deletions, and
a failure to conduct mRNA integrity analysis underlie the conclusion that 5' noncoding sequences in adenovirus late mRNAs facilitate ribosome initiation by utilizing sequences complementary to 18S rRNA.
This assertion ignores control Northern mRNA analyses presented in this
paper and elsewhere, and it improperly represents the size of deletions
introduced in the 5' noncoding region in such a way as to leave the
impression that they are nonspecific.
The examples cited above represent only a sampling of numerous
significant errors in the minireview published by Dr. Kozak. Careful
inspection of this minireview reveals a lack of scholarly accuracy that
will only serve to confuse and mislead readers. While Dr. Kozak is
entitled to her opinions, we believe very strongly that only
manuscripts of acceptable scholarly standards should be published in
Molecular and Cellular Biology.
Vadim I. Agol, Raul Andino,
Francis Bayard, Douglas R. Cavener, Stephen A. Chappell, Jane-Jane
Chen, Jean-Luc E. Darlix, Asim Dasgupta, Olivier Donzé,
Roger Duncan, Orna Elroy-Stein, Philip J. Farabaugh, Witold
Filipowicz, Michael Gale, Jr., Lee Gehrke, Emanuel Goldman,
Yoram Groner, Joe B. Harford, Maria Hatzoglou, Bin He,
Christopher U. T. Hellen, Matthias W. Hentze, John Hershey, Panda Hershey, Thomas Hohn, Martin Holcik, Craig P. Hunter,
Kazuei Igarashi, Richard Jackson, Rosemary Jagus, Leonard S. Jefferson, Bhavesh Joshi, Raymond Kaempfer, Michael G. Katze,
Randal J. Kaufman, Megerditch Kiledjian, Scot R. Kimball, Adi
Kimchi, Karla Kirkegaard, Antonis E. Koromilas, Robert M. Krug,
Veronique Kruys, Barry J. Lamphear, Stanley Lemon, Richard E. Lloyd, Lynne E. Maquat, Encarnacion Martinez-Salas, Michael B. Mathews, Vincent P. Mauro, Suzanne Miyamoto, Ian Mohr, David R. Morris, Eric G. Moss, Nobuhiko Nakashima, Ann Palmenberg, Neil
T. Parkin, Tsafi Pe'ery, Jerry Pelletier, Stuart Peltz, Tatyana V. Pestova, Evgeny V. Pilipenko, Anne-Catherine Prats, Vincent
Racaniello, G. Sullivan Read, Robert E. Rhoads, Joel D. Richter, Rolando Rivera-Pomar, Tracey Rouault, Alan Sachs, Peter Sarnow, Gert C. Scheper, Leslie Schiff, Daniel R. Schoenberg, Bert L. Semler, Aleem Siddiqui, Tim Skern, Nahum
Sonenberg, Wayne Sossin, Nancy Standart, Stanley M. Tahara,
Adri A. M. Thomas, Jean-Jacques Toulmé, Jeff Wilusz,
Eckard Wimmer, Gary Witherell, and Michael Wormington
The letter to the editor ignores or responds with lame defenses to
major points in my minireview. The letter diverts attention to side
issues, which I shall address, and ad hominem issues, which I shall
overlook. The letter to the editor was substantially rewritten after
the authors were shown a draft of this response. Because of that
unusual maneuver, their arguments appear to anticipate some of the
points below.
The first section of my minireview (39) questioned whether
appropriate criteria were used in identifying putative IRES elements in
cellular mRNAs. My main concerns in this regard, along with issues
raised in the letter, are discussed in the first section ("Does
internal initiation via IRES elements occur with cellular mRNAs?")
below. The second part of the minireview pertained to the claim that
some insect virus mRNAs initiate translation via a novel route that
does not require Met-tRNAi. This is discussed in the second
main section ("Initiation without Met-tRNAi?").
The third part of the minireview simply pointed out that it is too easy
to find, in various mRNAs, a short segment that is complementary to
rRNA. Invoking "elusive SD-like sequences" (25) enables one to imply base pairing between IRES elements and 18S rRNA
without even pointing to anything, but in some cases a particular mRNA
sequence has been singled out. I briefly discussed three examples: Gtx,
hsp70, and adenovirus late mRNAs. The main question is not how the
complementary sequence functions, which the letter to the editor
focuses on, but whether the complementarity is due merely to chance. In
none of these cases was the significance of the complementarity tested
by introducing point mutations. I think nothing more needs to be said.
Does internal initiation via IRES elements occur with cellular
mRNAs? (i) Vectors.
Given the absence of natural dicistronic mRNAs
that support independent translation of the downstream cistron, testing
for internal initiation requires constructing synthetic dicistronic mRNAs by transplanting a 5' untranslated region (UTR) to an internal position. My minireview raised two concerns about these artificial constructs. One big worry was whether a low-end positive result is
really a positive result. The letter responds to this concern in a way
that sidesteps the main issue. The letter argues that weak IRES
activity can be physiologically important because low-level translation
might be required to produce just the right amount of critical
regulatory proteins, such as c-sis. I completely agree that some
cellular mRNAs are designed to be translated poorly (21,
38), but if one wants to investigate the mechanism of that
low-level translation, one still needs an appropriate assay. The
scanning mechanism can be demonstrated even when it operates inefficiently (21, 41, 55, 58, 60). When testing for internal initiation, however, a low-end positive result using synthetic
dicistronic vectors is not credible for reasons explained in the next
paragraph. A better assay is needed. One cannot simply ignore the
limits of reliability of the assay on the grounds that it doesn't have
to work well. We still need to know what "it" is.
0270-7306/01/$04.00+0 DOI: 10.1128/MCB.21.23.8238-8246.2001
LETTERS TO THE EDITOR
LETTER
if she still wishes to oppose the ideato do so
openly. Needless to say, it is now difficult to mount a convincing case
for blanket repudiation of IRESs in the face of overwhelming data,
including elegant and compelling evidence from viral IRES-dependent
translation of a circular RNA (3), which was not cited in
the Kozak review.
-globin mRNA. They found that the eIF4G/4A complex binds the
EMCV IRES with an affinity sufficient for the IRES to be able to
compete with cellular capped mRNAs for eIF4F, a complex of factors
which contains eIF4G and helps to direct ribosome binding to capped
mRNA. While these data do not prove a mechanistic function, they
account for a critical first step. This reference was not cited by Dr.
Kozak, nor in fact was any of the literature that analyzed the
functional, specific interactions of eIF4G/4A/4F with EMCV-like IRESs
and of eIF3, another essential initiation factor that binds to the 40S
small ribosome subunit, with hepatitis C virus-like IRESs. True, these are viral IRESs. However, this is a well-known literature published in
leading journals, and it provides a quantitative and partial mechanistic understanding of IRES function that may be applied to
cellular IRESs.
FOOTNOTES
REFERENCES
1.
Bernstein, J.,
O. Sella,
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J. Biol. Chem.
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Carrasco, L.,
E. Battaner, and D. Vazquez.
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3.
Chen, C. Y., and P. Sarnow.
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Initiation of protein synthesis by the eukaryotic translational apparatus on circular RNAs.
Science.
268:415-417 4.
Eaton, B. J., and A. D. Steacie.
1980.
Cricket paralysis virus RNA has a 3' terminal poly A.
J. Gen. Virol.
50:167-171.
5.
Gallie, D. R.,
J. Ling,
M. Niepel,
S. J. Morley, and V. M. Pain.
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The role of 5'-leader length, secondary structure and PABP concentration on cap and poly(A) tail function during translation in Xenopus oocytes.
Nucleic Acids Res.
28:2943-2953 6.
Grundhoff, A., and D. Ganem.
2001.
Mechanisms governing expression of the v-FLIP gene of Kaposi's sarcoma-associated herpesvirus.
J. Virol.
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Hellen, C. U., and P. Sarnow.
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Internal ribosome entry sites in eukaryotic mRNA molecules.
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Huez, I.,
L. Creancier,
S. Audigier,
M. C. Gensac,
A. C. Prats, and H. Prats.
1998.
Two independent internal ribosome entry sites are involved in translation initiation of vascular endothelial growth factor mRNA.
Mol. Cell. Biol.
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Kozak, M.
2001.
New ways of initiating translation in eukaryotes?
Mol. Cell. Biol.
21:1899-1907 10.
Lomakin, I. B.,
C. U. Hellen, and T. V. Pestova.
2000.
Physical association of eukaryotic initiation factor 4G (eIF4G) with eIF4A strongly enhances binding of eIF4G to the internal ribosomal entry site of encephalomyocarditis virus and is required for internal initiation of translation.
Mol. Cell. Biol.
20:6019-6029 11.
Macejak, D. G., and P. Sarnow.
1991.
Internal initiation of translation mediated by the 5' leader of a cellular mRNA.
Nature.
353:90-94[Medline].
12.
Nanbru, C.,
I. Lafon,
S. Audigier,
M. C. Gensac,
S. Vagner,
G. Huez, and A. C. Prats.
1997.
Alternative translation of the proto-oncogene c-myc by an internal ribosome entry site.
J. Biol. Chem.
272:32061-32066 13.
Negulescu, D.,
L. E. Leong,
K. G. Chandy,
B. L. Semler, and G. A. Gutman.
1998.
Translation initiation of a cardiac voltage-gated potassium channel by internal ribosome entry.
J. Biol. Chem.
273:20109-20113 14.
Reavy, B., and N. F. Moore.
1981.
In vitro translation of cricket paralysis virus RNA.
Arch. Virol.
67:175-180[CrossRef][Medline].
15.
Sasaki, J., and N. Nakashima.
2000.
Methionine-independent initiation of translation in the capsid protein of an insect RNA virus.
Proc. Natl. Acad. Sci. USA
97:1512-1515 16.
Sella, O.,
G. Gerlitz,
S. Y. Le, and O. Elroy-Stein.
1999.
Differentiation-induced internal translation of c-sis mRNA: analysis of the cis elements and their differentiation-linked binding to the hnRNP C protein.
Mol. Cell. Biol.
19:5429-5440 17.
Stoneley, M.,
F. E. Paulin,
J. P. Le Quesne,
S. A. Chappell, and A. E. Willis.
1998.
c-Myc 5' untranslated region contains an internal ribosome entry segment.
Oncogene
16:423-428[CrossRef][Medline].
18.
Stoneley, M.,
T. Subkhankulova,
J. P. Le Quesne,
M. J. Coldwell,
C. L. Jopling,
G. J. Belsham, and A. E. Willis.
2000.
Analysis of the c-myc IRES; a potential role for cell-type specific trans-acting factors and the nuclear compartment.
Nucleic Acids Res.
28:687-694 19.
Wilson, J. E.,
T. V. Pestova,
C. U. Hellen, and P. Sarnow.
2000.
Initiation of protein synthesis from the A site of the ribosome.
Cell
102:511-520[CrossRef][Medline].
20.
Wilson, J. E.,
M. J. Powell,
S. E. Hoover, and P. Sarnow.
2000.
Naturally occurring dicistronic cricket paralysis virus RNA is regulated by two internal ribosome entry sites.
Mol. Cell. Biol.
20:4990-4999 21.
Yang, Q., and P. Sarnow.
1997.
Location of the internal ribosome entry site in the 5' non-coding region of the immunoglobulin heavy-chain binding protein (BiP) mRNA: evidence for specific RNA-protein interactions.
Nucleic Acids Res.
25:2800-2807 22.
Yueh, A., and R. J. Schneider.
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Genes Dev.
14:414-421
Robert Schneider
Department of Microbiology
New York University Medical School
New York, NY 10016
AUTHOR'S REPLY
requiring no explanationwhile a
2.5-fold increase is real. The increase was only 2.5-fold above
background when sequences from c-sis (3) or ornithine
decarboxylase mRNA (52) were tested. With six other
candidate IRES elements the stimulation was 
5-fold (Table 1 in
reference 39).
4-fold when the BiP sequence was inserted into, and judged against, an empty-vector control. The letter (paragraph six) inappropriately accuses me of
inappropriately comparing one BiP study (45) with another (66): I did not cite or discuss the second of those
studies at any time in any way. The straightforward studies I did cite showed 2.6-fold (37) or 4-fold stimulation (26,
36) when the BiP IRES was evaluated in vivo against an
empty-vector control.
Instead of faulting me for pointing out the quantitative discrepancies
in tests of the BiP IRES, I wish the letter had explained the reason
for starting with a vector that contains a 400-bp segment of the
Drosophila Antp gene. That vector is still in use
(16). Even more problematic is a dicistronic vector that
contains at the midpoint a mutated version of the EMCV IRES to which
candidate cellular IRES sequences were appended (5, 34). I
expressed concern that although the mutation in the EMCV insert
prevents it from functioning independently as an IRES, it might still
bind protein factors without which the test sequences would not have scored. Neither the letter nor the new review on internal initiation (25) offers any justification for using this vector which
seems to invite misinterpretation.
Control sequences inserted into the intercistronic region of a
dicistronic vector are not the only potential problem. The choice of
reporter genes and their arrangement (i.e., which is 5' and which 3')
can profoundly affect whether a putative IRES supports downstream
translation (27). It will be important to understand the
mechanisms behind the unexpected findings in that study of viral
(poliovirus and EMCV) and cellular IRES elements. RNA analyses, as
discussed next, might help.
(ii) RNA analyses. The second big concern I raised vis-a-vis synthetic dicistronic vectors was whether extraneous mechanisms (splicing, use of a cryptic promoter, or mRNA breakage) might subvert simple interpretation of the results even when activity is substantially (e.g., 10-fold) above background. The simplest interpretation is that if the 3' cistron gets translated, the intercistronic sequence is an IRES; but that assumes that the aforementioned extraneous mechanisms did not generate a monocistronic mRNA from which the downstream cistron is actually translated. Very careful RNA analyses are needed to rule out this possibility. Several points raised in the letter revolve around this issue.
The RNA analyses I am criticized for not citing were not determinative; the assays in those papers simply were not sensitive enough to prove the point. Routine RNA assays used to document presence of the intended dicistronic mRNA are not adequate to prove absence of an unintended monocistronic mRNA. According to one calculation explained in the minireview, even when an IRES supports 10-fold better translation of the 3' cistron than does the empty vector, that is only ~5% as efficient as translation from a capped monocistronic mRNA. Thus the RNA assay must be able to detectto rule outa monocistronic transcript
produced at 1/20 the level of the dicistronic form. Northern blots and
other routine RNA assays do not have that level of sensitivity. Even
greater sensitivity is required to rule out an internal promoter in the c-sis IRES, which supports translation only 2.5-fold better than the
empty vector.
The letter calls attention to my failure to cite controls in which
mutations in putative IRES sequences abolished translation of the 3'
cistron, but such mutations have little meaning without careful RNA
analyses. The question is not whether putative IRES activity is
sequence-specific but how the sequence functions. Consider some
examples.
- A putative IRES in eIF4G mRNA was shown by mutagenesis to require a polypyrimidine tract (20) that was later identified as a 3' splice junction sequence (22).
- The activity of the XIAP IRES was abolished upon deleting a polypyrimidine tract (Y10AG) that strongly resembles, but has not yet been shown to function as, a splice acceptor site (28).
- Recent analysis of alternative transcripts produced by the AML1 gene (43) revealed that the putative IRES from that gene includes a 3' splice junction sequence.
- The GC-rich VEGF IRES includes a proven transcriptional promoter (1). The authors of that study continue to call the VEGF sequence an IRES because there was residual low-level translation after the recognized promoter elements were deleted. As the letter (paragraph six) points out, however, "deletion of all transcription elements seldom completely abolishes [promoter] activity." The VEGF promoter was not recognized in another study (30), but the quality of RNA analyses therein certainly did not rule it out.
- The 1-kb long 5' UTR from human c-sis mRNA which is said to function as an IRES contains binding sites (GGGCGG) for transcription factor Sp1. The corresponding rat gene has been shown to produce a second transcript with a short 5' UTR initiated 15 nt upstream from AUGSTART (53), which suggests the presence of an internal promoter.
- The putative IRES in Gtx mRNA might also function as a promoter, although this has not been proved. The active component of the "IRES" (CCGGCGGGT) imperfectly resembles an Sp1 binding site. RNA analyses that could have tested the promoter hypothesis were not carried out with the construct in which expression was elevated by reiterating this GC-rich element (6).
(iii) Other issues. In addition to the experimental problems discussed above, a major theoretical problem is posed by the absence of conserved sequences among cellular IRES elements. As the list of putative IRES elements grows, the problem only becomes more glaring. Given the complete absence of structural criteria, internal initiation is just a vague category into which every anomalous observation can be thrown.
Detailed structural studies carried out on the c-myc sequence raised hope that, at least in one case, a real structure might be implicated in IRES function. The problem is that, after carefully defining a double pseudoknot near the 5' end of the mRNA (42), attempts to demonstrate the functional significance of the structure were disappointing. There was less than a two-fold reduction in internal initiation when the entire pseudoknot was deleted. Translation was reduced further, but still not abolished, when a downstream hairpin structure was also deleted. One of the loops has the sequence GGGAA (GGNRA), a stabilizing motif implicated in the function of many other folded RNAs; but substitution mutations in the c-myc hairpin loop actually augmented translation. The strongest decrease in translation was seen when an upstream AUG codon was inserted at various points in the c-myc sequence. The putative IRES element derived from the 5' end of c-myc mRNA is puzzling for other reasons. When transplanted to the midpoint of a dicistronic DNA vector, the c-myc sequence was shown to support efficient translation of the 3' cistron, and RNA analyses (which I did cite) detected no exculpatory monocistronic mRNAs. The problem is that the dicistronic mRNA failed to support translation of the 3' cistron when introduced through RNA transfection rather than the usual DNA transfection, implying the need for a nuclear experience. (The 5' cistron was translated in those experiments, so there was a good internal control. The negative result is meaningful.) I suggested that the required nuclear event might involve splicing or a cryptic promoter, i.e., production of a monocistronic mRNA that simply was not detected by the RNA assays. The letter suggests instead that the c-myc IRES might require nuclear binding proteins. Others have proposed that adenine residues might have to undergo methylation in the nucleus in order for the dicistronic mRNA to support translation (32). The proponents of these ad hoc explanations seem unwilling to consider the simplest possibilitythat the c-myc sequence
might not be an IRES. The wisdom of Sherlock Holmes seems worth
recalling. He advises that, when 9 out of 10 observations point in one
direction, the one discrepancy should be considered the strongest clue.
The efficiency with which a new candidate IRES supports downstream
translation is usually evaluated not by comparison to a normal
monocistronic mRNA but by comparison to a picornavirus IRES. This sets
the bar quite low, inasmuch as picornavirus sequences function poorly
in some tests of internal initiation (33; Fig. 4 in
reference 63). The usual rationale invoked for
internal initiation is that the scanning mechanism cannot function
efficiently when a 5' leader sequence has upstream AUG codons or
secondary structure, but that line of reasoning is undermined when the
internal initiation mechanism also functions poorly. The letter asserts that "IRESs have been shown to represent a range of activities from
weak to strong." The seemingly efficient cellular IRES elements, however, are mostly those for which RNA analyses are inadequate or
missing (Table 1 in reference 39).
Initiation without Met-tRNAi? The second section of my minireview concerned an unconventional mechanism of initiation postulated for some insect viruses. The experiments with Plautia stali intestine virus, which I cited only indirectly, showed that in vitro-synthesized capsid protein did not carry the usual N-terminal methionine (54). This was a provocative finding but it went no further. I focused on studies with CrPV because only in that case was a detailed mechanism proposed for initiating translation independently of Met-tRNAi (64). Much of that mechanism was based on toeprinting assays which to my eye did not show what was claimed regarding the position of the ribosome on the mRNA. The new review (25) recounts the "astounding" discoveries made with CrPV without responding to the questions I raised, point by point, about the toeprinting data. It would have been hard for Hellen and Sarnow (25) to address my concerns without even citing my review, which they did not.
In addition to toeprinting assays, the claim for a novel mechanism of translation rests on the fact that binding of CrPV mRNA to ribosomes was insensitive to standard inhibitors of initiation, such as L-methioninol and edeine. That insensitivity could mean either that initiation with CrPV mRNA follows a nonstandard pathway or that the observed mRNA-ribosome complexes are artifacts rather than functional intermediates in initiation. This issue clearly concerned the authors, who argued that the edeine-resistant complexes detected in sucrose gradients are not artifacts because actual translation of luciferase, when directed by CrPV mRNA, was also resistant to edeine. This was true, however, only at very low concentrations. Figure 3K in reference 64 shows that CrPV translation was inhibited (80%) by 1 µM edeine, which is within the range (1 to 10 µM) normally used to inhibit initiation of translation in eukaryotes. The letter tries to get around that result by arguing, in a confusing jumble of words, that 1 µM edeine inhibits the elongation phase of protein synthesis. The one study cited in support of that view used poly(U) as the template (4). Classical experiments showed that, with natural mRNAs, 1 µM edeine inhibits only the initiation step (31, 48). Those nontrivial experiments were conducted in a way that would have detected an effect on elongation, if such there were. Because edeine inhibits initiation and not elongation, it is frequently used to synchronize translation: after the first few minutes, 2 or 5 µM edeine is added to block further initiation so that various events that occur during elongationsuch as ribosomal
frameshifting or insertion of proteins into membranescan be studied
(29, 57, 59). Those experiments, carried out in many
different laboratories, would not have worked if edeine inhibited elongation.
If one accepts that edeine inhibits only the initiation step, the
argument regarding the authenticity of complexes detected by sucrose
gradient analysis gets inverted. Because actual translation of
luciferase directed by CrPV mRNA was sensitive to inhibition by 1 µM
edeine (Fig. 3K in reference 64), the
edeine-resistant complexes detected in sucrose gradients are likely to
be artifacts. Nonfunctional sticking of CrPV mRNA to ribosomes could
also explain the partial resistance to L-methioninol. The
logic that applies when initiation complexes are sensitive to
L-methioninol (40) does not hold when
ribosome-mRNA complexes are resistant to the inhibitor.
The mechanism proposed for CrPV postulates that, without the usual
binding of Met-tRNAi in the P-site, translation initiates with entry of Ala-tRNA into the A site. I suggested this should be
tested directly by looking for binding of Ala-tRNA to CrPV mRNA-ribosome complexes. A positive result would support the claim that
the complexes are functional. But that challenge received no response.
Instead, because I used the word "aggregate" in that paragraph of
the minireview, the letter jumps on me for questioning the oligomeric
state of the RNA. As I used the word, "aggregate" clearly refers to
nonfunctional complexes in which mRNA is merely adsorbed to the
ribosome. I clearly was not questioning whether the mRNA per se was
aggregated. This is an example of how the letter diverts attention to
irrelevant side issues while ignoring the substantive concerns raised
in the minireview.
The fact that CrPV capsid protein can be translated in vitro from
genomic RNA could be an artifact, inasmuch as in vitro translation systems sometimes allow internal initiation that does not reflect what
happens in vivo (2, 21, 24, 46, 56). In vitro translation
of CrPV capsid protein via the putative IRES was inefficient (e.g.,
Fig. 6 in reference 65), which is grounds for
questioning its authenticity. In vitro translation using mRNA from a
related insect virus was also inefficient and inexact (Fig. 2 in
reference 13). When cellular IRES elements function
poorly, one can argue that cells might not need much of the protein,
but viral capsid proteins are needed in large quantities. That is why
so many other viruses in which the capsid protein is encoded at the 3'
end of the genome produce a subgenomic mRNA.
Perhaps I should have mentioned a study by Eaton and Steacie
(14) in which no subgenomic mRNA was detected by labeling
CrPV-infected cells with [3H]uridine for 3 h, but I
omitted the reference because the technique was not sensitive enough to
prove the point. It is not fair to criticize a study from 20 years ago
that used the best technique then available; it is fair to expect a key
point to be reinvestigated using sensitive, modern techniques. The
Northern blot proffered by Wilson et al. (65), which
examined RNA from one unstated time point in the infection, is far from
adequate to prove absence of a subgenomic mRNA. Wouldn't it be better
to look carefully for a subgenomic mRNA than to claim the question was
settled by "compelling and rigorous" experiments from 20 years ago?
I don't know why the low-level in vitro translation of these insect
virus RNAs requires preservation of the pseudoknot. It could be
something as trivial as targeting an RNase (15), or the
structure really might be an IRES. In vitro translation clearly occurs
in the absence of an AUG codon, which is surprising and interesting
even if a more conventional mechanism turns out to operate, via a
subgenomic mRNA, in vivo. I did not claim to have disproved that an
unusual mechanism of initiation operates with these viruses. I said
only that the experiments in reference 64 had
serious deficiencies and therefore the postulated mechanism awaits proof.
Closing notes. The letter to the editor exposes no relevant issues that were ignored in my minireview. I did not discuss the literature on initiation factors because no candidate IRES of cellular origin has been shown to bind eIF4G or other initiation factors. Even if an initiation factor were shown to bind (several of the factors are general mRNA-binding proteins), it would prove little without functional tests, i.e., evidence that the prebound factor can mediate ribosome entry. That chase experiment has not yet been carried out with EMCV RNA to verify that the tight binding of eIF4G/4A (44) has functional consequences.
The letter condemns my failure to discuss putative IRES elements in viral mRNAs, but my short review was focused on cellular mRNAs. If a review is to be condemned for omissions, attention might be directed to lengthy reviews of viral translation (17, 50) that make no mention of the polycistronic mRNAs produced by adenoviruses, papovaviruses, retroviruses, coronaviruses, hepatitis B virus, brome mosaic virus, tobacco mosaic virus, etc. All these viruses produce polycistronic mRNAs in which the downstream cistrons are silent because of constraints imposed by the scanning mechanism. The silent cistrons are activated upon being relocated to the 5' end of smaller transcripts. Reviews that ignore this remarkable body of literature while extolling the slightest hint of internal initiation give students a distorted view of how translation operates in eukaryotes. I agree that the hairpin test mentioned in the letter would be a good alternative test for internal initiation, if it were accompanied by careful RNA analyses to ensure that the hairpin barrier is not circumvented by mRNA breakage or splicing or a downstream promoter. But the hairpin test is usually used as a shortcuta substitute for
carefully monitoring mRNA structureand for that reason it is not
determinative. Circularization of the mRNA would also be an excellent
alternative test for internal initiation, but since that test has not
been employed with any cellular IRES sequence, it seems unfair to fault
me for not mentioning it. Indeed, the circularization test has not been
attempted with any viral IRES other than EMCV.
The accusation that the minireview contains "numerous distortions of
fact and of published data" would be serious, if true, but the letter
misrepresents what I said in an attempt to prove the charge. In the
discussion of vectors (see above), for example, what I actually said
about tests of the BiP IRES in no way resembles what the letter
asserts. The letter accuses me of not presenting the data in reference
23 "fully and accurately," but because that
paper concerns a viral IRES, it was not discussed at all in the
minireview. It is the letter to the editor, not my minireview, that
misrepresents established facts about edeine by invoking a result
obtained with poly(U) that does not apply to natural mRNAs. The letter
condemns my failure to cite various control experiments which, as
explained above, simply did not prove what was claimed.
A scholarly review is not one that cites every paper but one that
thoughtfully re-views what has been published. When the papers
pertaining to internal initiation are stacked on one's desk, the pile
looks overwhelming. But when the data are extracted and spread out in
table formhow active was the sequence, what was the baseline,
etc.holes become apparent. Not every paper had the same flaw, but
almost every paper had a major flaw or uncertainty (39).
An overwhelming stack of papers does not equate with overwhelming
proof. The letter defends these papers on the grounds that they were
published in prominent journals. I wrote the minireview as a plea for
stricter standards by those journals, whose editors now have a
convenient list to check against when selecting referees.
When my minireview was submitted for publication, one of the referees
who evaluated the manuscript wrote as follows: "I think the valid
criticisms raised here are generally recognized by the major
researchers in the translation field (although not always followed!).
Therefore this audience will learn little or nothing new. For those
outside the field, the review may inappropriately cause them to dismiss
the possibility of alternate mechanisms of initiation, which would be a
disservice to the scientific community." That referee's advice was
disregarded perhaps because the editor believes, as I do, that people
outside the fieldpeople who attempt to put the "alternate
mechanisms" to workare entitled to know the problems.
I will save the curious reader the trouble of counting the names
appended to the Letter to the Editor: there are 87 votes in favor of
cellular IRES elements and associated phenomena. Some of the signers
(e.g., Drs. Farabaugh, Filipowicz, Goldman, and Krug) work on subjects
completely unrelated to the content of the minireview; they must have
studied hard to qualify as judges. The letter was composed and
circulated by Drs. Schneider and Sonenberg. Many of the signers have
close links to Dr. Sonenberg, either as coauthors or members of the
same institution.
It is obvious that the organizers worked hard to collect all those
signatures, but to what end? A single voice suffices to present a
logical argument. I might be alone in refusing to believe a story with
so many flaws, but that does not mean I am wrong. Counting the votes
determines the answer in politics (Florida excepted) but not in science.
| |
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Marilyn Kozak Department of Biochemistry Robert Wood Johnson Medical School 675 Hoes Lane Piscataway, NJ 08854 |
Molecular and Cellular Biology, December 2001, p. 8238-8246, Vol. 21, No. 23
0270-7306/01/$04.00+0 DOI: 10.1128/MCB.21.23.8238-8246.2001
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