Fine words butter no parsnips

One more cellular IRES has been discovered, so I have to abandon my duties and waste my precious time...

Daba, A., Koromilas, A. E. & Pantopoulos, K. Alternative ferritin mRNA translation via internal initiation. RNA (2012).doi:10.1261/rna.029322.111 [can be found ahead of print here].

H-ferrtin expression is known to be transcriptionally up-regulated under a variety of conditions, including oxidative stress. Inhibition of translation under the latter case is well-documented and is attributed to eIF2 phosphorylation. Authors addressed whether H-ferritin mRNA translation could be resistant to translation inhibition.
First, they utilized inducible PKR to inhibit eIF2-dependent translation. Addition of coumermycin induced fusion PKR-GyrB dimerization and autophosphorylation of PKR which, in turn, phosphorylated eIF2 (Figure 1A). This resulted in profound inhibition of protein synthesis (polysomes in Figure 1B and [35S]-Met incorporation in Figure 1C, compare lanes 1 and 2). De novo translation of H-ferritin was also dramatically inhibited! But the authors prefer to express this in other words:

nevertheless, newly synthesized [35

S]-ferritin could be partially recovered in the immunoprecipitate.

OK, and what were the controls, you may well ask? The sad thing is that no control is provided (or was performed). How β-actin is inhibited? To a similar extent or stronger? Or maybe less stronger? Treatment with hemin enhanced ferritin [35S]-labeling with or without coumermycin. Optically (no quantification is provided) there is similar inhibition in both cases. But the authors summarize:

These data suggest that ferritin mRNA possesses the capacity to, at least partially, bypass the translational blockade imposed by eIF2a phosphorylation.

But without controls this can’t be said. 1 to 0. Referees suck.

Next, pulse-labeled [35S]-ferritin was precipitated from cells infected with attenuated poliovirus. The latter is known to express 2Apro that cleaves eIF4G. Indeed, eIF4GI was cleaved, eIF2 was phosphorylated (Figure 2A), and less ferritin were synthesized (Figure 2B). If anyone (but referee) compares how strong is stimulation of ferritin expression by hemin in figures 1C and 2B, he will be definitely surprised. In the former case there’s 2-3-fold stimulation, but in the latter one the stimulation extent is huge, to say the least. Where’s the truth? Fig.2B looks more similar to what these authors published before, but, anyway, it’s minor point. And again authors say:

These findings provide additional evidence that de novo ferritin synthesis is possible under conditions where global protein synthesis is shut down.

No control is provided for sure. Neither we know if eIF4GII is cleaved under these experimental conditions (time-course of eIF4GI/II cleavage is well-known for w/t poliovirus, but not for Sabin I strain), nor how other proteins’ synthesis is affected (quantitatively). No controls. 2 to 0. Referees suck.

Next, mRNA distribution in polysomes was addressed under normal conditions and after PKR induction.

1. PKR reduces ferritin mRNA contents in heavy polysomes. This is in line with translational repression.
2. Hemin treatment shifts this mRNA into heavier fractions which suggests translational upregulation by the way, but the authors did not pay attention to this fact.
3. Combined action does not have any pronounced effect, which is not surprising, you know. If you have two diametrically opposed actions, their mutual cancellation is not unexpected.
4. β-actin mRNA distribution is only affected by PKR activation, and inasmuch as β-actin transcription is not affected by hemin, the combined treatment is inhibitory.

But the authors say:

These results indicate an enhanced capacity of ferritin mRNA to bypass a translational blockade under stress conditions.

To say this you must be either cheating, or stupid, or both. 3 to 0. Referees suck.

Needless to say, Figure 4 fails to impress either. Authors used tet-responsive FLAG-IRP mutant which is constitutively active but not able to inhibit ferritin translation at high cells densities (Wang, J. & Pantopoulos, K. Conditional derepression of ferritin synthesis in cells expressing a constitutive IRP1 mutant. Mol Cell Biol 22, 4638–4651 (2002)). TfR1 or GADPH were supposed to represent controls. TfR1 is known to be inhibited by this IRP mutant. Authors pelleted polysomes in w/t or IRP-overexpressing cells, then immunoprecipitated them with anti-FLAG antibodies and addressed whether ferritin/TfR1/GADPH mRNA was present in the precipitate. Indeed, ferritin and TfR1 mRNAs could be detected. But does it extend our knowledge? Very subtly. And again, no controls.

Demonstration of “bona fide IRES” in the end of the manuscript is methodologically OK in terms of XX century. Unfortunately, these good ol’ times are gone. And in the XXI century we know that without comparison of monocistronic vs. bicistronic, or m7G-capped vs. A-capped mRNAs any IRES research is incomplete. No IRES is demonstrated. In figure 7 there must be Fluc/Rluc ratio presented, rather than Rluc/Fluc one, and 16 hours is too long for RNA transfection. And no positive control is provided.

Nowadays people seem not to be able to work thoroughly. They do not know what control is and why it is required. Is it something about education? And referees are either stupid, or unobservant, or most likely both. And the same referees publish similarly poorly performed researches. And it’s bad for ya.

If this were play'd upon a stage now, I could condemn it as an improbable fiction.

One more manuscript made me itching recently...


Thakor, N. & Holcik, M. IRES-mediated translation of cellular messenger RNA operates in eIF2α-independent manner during stress. Nucleic Acids Res (2011). doi:10.1093/nar/gkr701[PubMed]


XIAP IRES is studied in rabbit reticulocyte lysate. RRL is known to produce artifacts when it comes to internal initiation study so a lot of fun was anticipated.
A few questions to warm up. WTFhat on Earth is "ORF (35 nt)" (Figure 1A)? Does it encode not integer number of aminoacids or maybe it encodes frame-shift site? Promega users would be happy to know that now they can purchase a new product: RNAsein.


First, authors wanted us to believe that RRL is suitable to study XIAP translation. They utilized toeprinting approach. And indeed toe-prints were seen. But then come controls.

First, the initiation codon AUG was mutated to AAC (highlighted by a circle in Figure 2A; referred to as Start Codon, SC, mutant). The 40S leading edge toeprints were not observed with the SC mutant (Figure 2B, lane 4).

Well... Although I have to wear spectacles (or maybe due to this fact) I can see some toe-prints in the Figure 2B, line 4, though they are weaker, I have to admit. The very fact that the toe-prints are nevertheless observed on ACC codon is alarming. And even more alarming is the fact that reviewers of this manuscript have not bothered themselves to inspect a figure.

Second, the substitution of UU to AA in the polypyrimidine tract (PPT) of XIAP IRES (highlighted by a rectangle in Figure 2A) <revealed> the inability of the XIAP IRES PPT mutant to form an initiation complex. Strikingly, the PPT mutant was able to form an initiation complex once a m⁷G-cap was added to the 5'-end of the in vitro transcribed RNA.

One can see spots, which correspond to the full-length reverse transcription products (the bottom of Figure 2B). And the spot in lane 3 is much thicker than those in neighbor lanes. This fact has rather simple explanation: there's more cDNA synthesized in this reaction. And thicker toe-print reflects not the better 48S-complex assembly, but rather sloppy performance of the scientist. Moreover, on the Figure 2A I can see two uAUGs in the XIAP 5'UTR. And the context of one of them is considerably improved by this mutation: AUGU is transformed to AUGA. Kozak context, you might have heard of this... If translation on XIAP mRNA is initiated via scanning, this would perfectly explain loss of authentic toe-print. Also, this is very nice internal control. If in RRL toe-prints of similar intensity can be found on all AUG-codons, not only on authentic one... Then RRL sucks. Unfortunately, this part of the gel is not shown.

Strikingly, the uncapped wt XIAP IRES RNA was able to form an initiation complex in the poly I:C-treated RRL (Figure 3B, lanes 2 and 3), and in fact the fluorescence intensity of the 40S leading edge toeprints was enhanced by poly I:C treatment (Figure 3B, lanes 2 and 3).

If one compare lane 1 (supposed to be a control) and lanes 2 and 3 (where poly I:C was added), indeed there are pronounced toeprints after poly I:C addition. However, in the control reaction no ATP was added. This makes such control irrelevant, since two parameters were changed, while only one parameter may be changed. Moreover, if we look in Figure 1C, we can notice that addition of ATP in fact stimulates toe-prints. So was it poly I:C or ATP addition that enhanced toeprint?
One more point. There's more full-length cDNA in "XIAP + poly I:C + GTP" lane (see note above). Therefore, we have no reason to assume that RRL is suitable for XIAP studies. And we have no reason to assume that phosphorylation of eIF2 stimulated XIAP translation in RRL.
Next experiment is not reliable either. Authors tried to prove the identity of toe-prints. Usually, 48S or 80S complexes are purified from sucrose gradient, then reverse transcription is performed (1). Such approach can show us that:

1. One ribosome is bound to mRNA (in from of 48S or 80S).
2. This ribosome is positioned exactly on the authentic AUG-codon. 

The authors, however, purified something via streptotag introduced into the XIAP mRNA, then confirmed presence of ribosomes on this mRNA, and again performed toe-printing. Contrary to the approach described above, this only demonstrates that:

1. There are ribosomes on XIAP mRNA.
2. Some of these ribosomes are positioned on the authentic AUG-codon.

Feel the difference. Moreover, authors supplemented RRL with ribosomes from HeLa. What was the source of the ribosomes? Can one be sure that those ribosomes are devoid of initiation factors contaminations?

At the moment we know two alternative pathways of the initiator tRNA delivery to the ribosome: eIF5B-mediated delivery on HCV-like IRESs and eIF2D-mediated one in this and some other cases. Quite logically, therefore, the authors tried to address the possibility that one of these mechanisms could operate on XIAP mRNA. They show that depletion of eIF2 and eIF5B strongly inhibits 48S-complex formation on the XIAP mRNA. But no control is provided. How would other mRNAs behave? Thus from this experiment we may not deduce any specific translational properties of XIAP mRNA.

Next, the authors performed RNAi against eIF5B and found no decline in endogenous XIAP or b-actin levels. So they added poly I:C to the cells treated with anti-eIF5B siRNA and found that XIAP level is decreased.

It is known, however, that XIAP stability is regulated during apoptosis (see e.g. ref. 2,3). And apoptosis can be induced by poly I:C (see e.g. ref. 4). This issue is not addressed. Therefore, authors' thesis is not proven.

Next point is ridiculous. The authors wrote:

Pestova et al. (5) reported that eIF5B is dispensable to form elongation competent 80S initiation complex on CSFV IRES.

Read the paper (5). eIF5B is strictly required for both eIF2-dependent and - obviously - for eIF2-independent mechanisms. Just read the paper.


So the bottom line is:

1. Control experiment may only differ from test point by one parameter.
2. When addressing toe-prints, it is important to make sure that all other RT-stops except stops from a ribosome are identical both quantitatively and qualitatively.
3. Read thoroughly and think permanently.

I would not even say that this is not the level of NAR. Such manuscripts should not be published at all, because in the absence of proper controls no experiment should be published. And the reviewers (if there were any) are simply unqualified. Sad but true. The referees must be expelled to Saudi Arabia where they will have their hands chopped off. And then decapitated.

1. Anthony, D.D. & Merrick, W.C. Analysis of 40S and 80S complexes with mRNA as measured by sucrose density gradients and primer extension inhibition. J Biol Chem 267, 1554–1562 (1992).
2. Wen-Hsien Liu, Huey-Wen Hsiao, Wen-I Tsou and Ming-Zong Lai. Notch inhibits apoptosis by direct interference with XIAP ubiquitination and degradation. The EMBO Journal (2007) 26, 1660 - 1669.

3. Dan, H.C. et al. Akt phosphorylation and stabilization of X-linked inhibitor of apoptosis protein (XIAP). J Biol Chem 279, 5405–5412 (2004).

4. Dufour, F., Bertrand, L., Pearson, A., Grandvaux, N. & Langelier, Y. The ribonucleotide reductase R1 subunits of herpes simplex virus 1 and 2 protect cells against poly(I · C)-induced apoptosis. J Virol 85, 8689–8701 (2011).

5. Pestova, T.V., de Breyne, S., Pisarev, A.V., Abaeva, I.S. & Hellen, C.U.T. eIF2-dependent and eIF2-independent modes of initiation on the CSFV IRES: a common role of domain II. EMBO J 27, 1060–1072 (2008).

We'll discover our own IRES, with blackjack and hookers! :)

Probably I should beg pardon in advance for a mocking way of discussion, it is explicitly expressed that authors of this blog have no intention to offend anybody. Tonight we dissect
Dai, N. et al. mTOR phosphorylates IMP2 to promote IGF2 mRNA translation by internal ribosomal entry. Genes Dev (2011) 25: 1159-1172. [PubMed]

What do we have? Translation of IGF2 mRNA with L4 leader is not affected by rapamycin treatment, while that with L3 leader is (Figures 1A and 1B). Next, overexpression of eIF4E (3-fold over endogenous protein) does not affect translation driven by both leaders (Figure 1C). And, finally, overexpression of nonphosphorylatable 4E-BP1 variant doesn't inhibit both mRNAs (Figure 1D). The authors make a bit unexpected conclusion:
These results indicate that, despite its complex secondary structure, the L3-luciferase mRNA is translated in an eIF-4E-independent manner.

What? English, motherfucker! Do you speak it? (c) Two mRNAs. None is stimulated by eIF4E overexpression. None is inhibited by 4E-BP overexpression. But one of them is translated in an eIF4E-independent fashion, while another is not. Too complex for me to understand...
As a control, authors utilized ODC (ornithine decarboxylase). Rather unwise (or sneaky) control - and again lights are on but no referee is at home. Overexpression of eIF4E stimulates endogenous ODC expression. But it also stimulates ODC mRNA export (1) so cumulative effect is observed and ODC simply can not be used as a positive control for eIF4E and/or 4EBP effects on translation, unless it is transfected as an RNA.
After this striking finding what could be more logical than to look for an IRES? Indeed authors made bicistronic plasmids with L3 leader (L4 leaders would be an instructive control) in the intercistronic position. Authors found that L3 leader promotes internal translation 15 times better that b-globin leader, "expression of the latter being negligible". 15 multiplied by "negligible" equals to negligible, from math's point of view. If we compare b-globin to any conventional IRES, say, EMCV, the latter works 100-1000 times better, depending on cell line.
The acid test for any "IRES" is whether expression from an artificial bicistronic mRNA could be physiologically relevant. And since all those cellular IRESs are naturally capped and monocistronic, the idea is to compare expression levels from m7G-capped monocistronic and bicistronic mRNAs (2,3). So, authors employed RNA transfection to show that 24 hours after transfection... Stop! Does anybody know how many RNA remains in cell a day(!) after transfection. Look at Figure 3C from (4). There's about 85-90% of initially transfected mRNA being lost. So what do you measure when almost none of the input mRNA remains? I don't know. But it's not the only trouble. mRNAs were transfected with Lipofectamine (it's not the antiadvertising, I use it myself), but in the course of lipofection most of the transfected mRNAs are confined in cellular compartments (not reaching cytoplasm!) and their apparent identical stability (see Suppl. Figure 3) is just an artifact (see ref. 5). 
But maybe luciferase values are decisive and unambiguous? In bicistronic mRNA with "L3 IRES" Fluc/Rluc ratio is ~0,15. Is it good or bad? In the absence of negative and positive controls there's no answer. But I can give you a hint: in HEK293T cells the same ratio for bicistronic EMCV mRNA is ~0,05 (note that relative activities of both luciferases - light units per molecule - are distinct). So "L3 IRES" is 3-fold more active than EMCV IRES. Does it correlate with the results of DNA transfection? Ask the referees...
There's one more tricky thing. Much more tricky. L3-Fluc mRNA translation is not stimulated by the cap (Figure 2D and Suppl. Figure 3) and is equally effective in mono- and bicistronic mRNAs. This would suggest an IRES, but 24 h is too much. I would believe in IRES if the same results can be demonstrated 2-4 hours post transfection with A-cap as a control (see below).  
The next part of the manuscript is more profound. Authors find that:

1. Rapamycin inhibits binding of IMP2 to L3, but not L4 leader
2. Overexpression of IMP2 stimulates - and RNAi against IMP2 inhibits - expression of L3-IGF2, but not that of L4-IGF2. Since DNA transfection was performed, we can only say expression, but not translation.
3. Overexpression of IMP2 relieves inhibition by rapamycin.
4. IMP2 is phosphorylated by mTORC1.
5. Mutation of Ser162 and Ser164, which are phosphorylated by mTORC1, to alanines inhibits binding of IMP2 to L3 leader. This fact should be taken with caution. Well-known story is mutation of allegedly phosphorylated Ser53 of eIF4E to alanine which appeared to fuck overall eIF4E structure up, rather than mimic unphosphorylated eIF4E.
6. Expression of phosphomimetic Ser162/164Asp, however, resulted in inability of rapamycin to inhibit L3-driven translation.

So what do we have?
mTORC1-dependent binding of IMP2 stimulates translation of L3-IGF2 mRNA. But that's all, folks.
To prove the title of the paper "mTOR phosphorylates IMP2 to promote IGF2 mRNA translation by internal ribosomal entry" it would be nice to:

1.  Perform RNA transfections to compare efficiencies of monocistronic vs. bicistronic mRNA translation, but to assay luciferases' activity 4 hours post transfection.
2. Compare not methylated vs. unmethylated mRNAs, but m7GpppG-capped vs. ApppG-capped ones. I'm not aware of effective cytoplasmic guanylyl-transferase activity, but in cytoplasmic extracts there's plenty of it (probably it' a contamination)!
3. Include bicistronic L4 mRNA in all tests and provide adequate positive and negative coctrols.
4. If all described in the manuscript is true, it should also work in vitro, HeLa extracts are easy to purchase or even to make by yourself. Invariable DNA transfections are a bit suspicious.
5. Effect of rapamycin/IMP2 on bicistronic mRNA, bearing L3 leader between luciferases.

In fact, forget the IRES (for a while)...


1. Rousseau, D., Kaspar, R.L., Rosenwald, I., Gehrke, L. & Sonenberg, N. Translation initiation of ornithine decarboxylase and nucleocytoplasmic transport of cyclin D1 mRNA are increased in cells overexpressing eukaryotic initiation factor 4E. Proc Natl Acad Sci USA 93, 1065–1070 (1996).
2. Elango, N., Li, Y., Shivshankar, P. & Katz, M.S. Expression of RUNX2 isoforms: involvement of cap-dependent and cap-independent mechanisms of translation. J Cell Biochem 99, 1108–1121 (2006).
3. Andreev, D.E. et al. Differential contribution of the m7G-cap to the 5' end-dependent translation initiation of mammalian mRNAs. Nucleic Acids Res 37, 6135–6147 (2009).
4. Lourenço, S., Costa, F., Débarges, B., Andrieu, T. & Cahour, A. Hepatitis C virus internal ribosome entry site-mediated translation is stimulated by cis-acting RNA elements and trans-acting viral factors. FEBS J 275, 4179–4197 (2008).
5. Barreau, C., Dutertre, S., Paillard, L. & Osborne, H.B. Liposome-mediated RNA transfection should be used with caution. RNA 12, 1790–1793 (2006).