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 (1-21,1-38), 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 (1-21, 1-41, 1-55, 1-58, 1-60). 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.

The question when using dicistronic vectors is this: if translation of the 3′ cistron preceded by a candidate IRES sequence is close to background level, is it anything more than background variation? The problem is that the “negative control” (empty vector) is never negative. There is always some expression of the 3′ gene. Without understanding how that translation is achieved (via mRNA breakage? via a cryptic promoter?), everyone simply sets it at 1.0 and looks for expression greater than 1.0 when the candidate IRES is inserted. Extraneous sequences that merely lengthen the intercistronic region have been shown to elevate background translation of the 3′ cistron as much as 10-fold (Fig. 9 in reference 1-18), perhaps by providing room for RNases to cleave and thus release a translatable 3′ RNA fragment. The variability in and uncertain cause of the background expression set limits on the reliability of the dicistronic assay.

The analogy to transcriptional promoters is an inappropriate defense for IRES elements that score barely above background. With a promoter, there might be uncertainty about which sequences or which factors mediate transcription but the basic mechanism is not in question. With candidate IRES elements that function close to background level, however, the uncertainty is fundamental: are we seeing internal initiation of translation or just a slight increase in the undefined mechanisms that generate background? It is not natural dicistronic mRNAs that are being studied. These are artificial constructs in which a 5′ UTR has been inserted between two convenient reporter genes. It seems injudicious to argue that a certain level of translation of the 3′ cistron is just background—requiring no explanation—while a 2.5-fold increase is real. The increase was only 2.5-fold above background when sequences from c-sis (1-3) or ornithine decarboxylase mRNA (1-52) were tested. With six other candidate IRES elements the stimulation was ≤5-fold (Table 1 in reference 1-39).

The letter misrepresents my position on a related issue. I did not make a broad assertion “in the absence of any evidence to support [my] view” that IRES elements give positive results only because the IRES replaces an inhibitory control sequence. I raised that possibility specifically in connection with BiP (1-45), where the negative control was not the usual empty dicistronic vector but one into which a 400-bp inverted segment of the Drosophila Antpgene was inserted between the 5′ and 3′ cistrons. It is an unusual starting point. Upon replacing the Antp sequence with the BiP IRES, translation of the 3′ cistron was stimulated 15- to 30-fold (1-45); but the stimulation was ≤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 (1-45) with another (1-66): 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 (1-37) or 4-fold stimulation (1-26,1-36) 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 theDrosophila Antp gene. That vector is still in use (1-16). 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 (1-5, 1-34). 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 (1-25) 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 (1-27). 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 detect—to rule out—a 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 (1-20) that was later identified as a 3′ splice junction sequence (1-22).

• 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 (1-28).

• Recent analysis of alternative transcripts produced by the AML1 gene (1-43) revealed that the putative IRES from that gene includes a 3′ splice junction sequence.

• The GC-rich VEGF IRES includes a proven transcriptional promoter (1-1). 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 (1-30), 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 AUG^START (1-53), 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 (1-6).

In short, the fact that a certain sequence allows downstream translation, while various controls do not, does not prove that the sequence that works is an IRES.

There are other reasons to worry about inadvertent production of spliced mRNAs from dicistronic vectors. The RP vector designed by A. E. Willis has been used to identify many candidate IRES elements (1-6, 1-7, 1-8, 1-9, 1-35, 1-51, 1-61, 1-62). An intron built into this vector upstream from the first cistron might make it easy to generate a surreptitious monocistronic mRNA: the candidate IRES need contribute only a cryptic 3′ splice site. Inadvertent splicing indeed occurred with the Willis vector in at least one case (1-51), although internal initiation was said to persist after removal of the intron. The vector used to test for IRES activity in NRF mRNA also has an upstream intron (1-49). The importance of careful RNA analyses is illustrated by a viral system in which a dicistronic vector unexpectedly produced both dicistronic and monocistronic mRNAs (1-23). Production of the spliced, monocistronic transcript occurred much more readily with LUC as the 3′ cistron than with the natural viral gene, which is noteworthy given the frequent use ofLUC as the reporter gene. The authors speculated that translation of the natural viral gene occurs primarily from the dicistronic mRNA because the monocistronic mRNA is scarce in latently infected cells, but the fact that the monocistronic mRNA increases when lytic infection is induced (Fig. 4 in reference 1-23) complicates the judgment.

The letter (paragraph seven) mentions studies in which “in vitro synthesized mRNAs … were monitored in cell-free systems or examined after expression in cultured cells, and the RNAs were found to be intact.” I don't know what this broad, undocumented statement means. Cellular IRES elements usually do not support translation efficiently in cell-free systems (1-32). In rare cases where a cellular IRES did allow efficient translation of the 3′ cistron in vitro, no attempt was made to show that the dicistronic mRNA remained intact (1-7, 1-47). The translatability of dicistronic mRNAs in vivo is what counts, and, for the reasons outlined above, the absence of unintended monocistronic transcripts certainly has not been proved in most cases.

The letter asserts that “Kozak is not alone in expressing concern” about the need for careful RNA analyses. Indeed, the new review by Hellen and Sarnow (1-25) has a nicely worded paragraph about the importance of determining that a vector produces only the intended dicistronic mRNA, but it is only lip service. Their table of cellular IRES elements makes no distinction between really careful studies (p58^PITSLRE [1-10]), studies that addressed the RNA issue via very, very faint Northern blots (Cat-1 and DAP5 [1-16, 1-26]), and studies that included no analysis of RNA structure at all (MYT2 and eIF4G [1-19, 1-36]).

The new review (1-25) extols a developmentally controlled IRES in fibroblast growth factor 2 mRNA, but that report (1-11) and similar studies with the c-myc IRES (1-12) did not establish that the dicistronic vector produces only dicistronic mRNA in mouse tissues that show translation of the 3′ cistron. Both reports included RNA analyses that documented the amount but not the form of mRNA. A tissue-specific or stage-specific IRES would be extremely interesting, but this should not be claimed until other explanations (tissue-specific splicing, tissue-specific promoters) have been ruled out. Is the “scholarly” review the one that repeats the premature claim or the one that explains why it is premature?

(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 (1-42), 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 (1-32). The proponents of these ad hoc explanations seem unwilling to consider the simplest possibility—that 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 (1-33; Fig. 4 in reference 1-63). 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 1-39).

Initiation without Met-tRNA_i?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 (1-54). 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-tRNA_i (1-64). 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 (1-25) 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 (1-25) 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 asl-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 1-64 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 (1-4). Classical experiments showed that, with natural mRNAs, 1 μM edeine inhibits only the initiation step (1-31, 1-48). 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 elongation—such as ribosomal frameshifting or insertion of proteins into membranes—can be studied (1-29, 1-57, 1-59). 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 1-64), 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 tol-methioninol (1-40) 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-tRNA_i 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 (1-2, 1-21, 1-24, 1-46, 1-56). In vitro translation of CrPV capsid protein via the putative IRES was inefficient (e.g., Fig. 6 in reference 1-65), 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 1-13). 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 (1-14) 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. (1-65), 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 (1-15), 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 1-64 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 (1-44) 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 (1-17, 1-50) 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 shortcut—a substitute for carefully monitoring mRNA structure—and 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 reference1-23 “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 form—how 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 (1-39). 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 field—people who attempt to put the “alternate mechanisms” to work—are 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.