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Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: Twitter: Dereklowe

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February 24, 2014

Another Round of Stapled Peptide Wrangling

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Posted by Derek

When we last checked in on the Great Stapled Peptide Wars, researchers from Genentech, the Walter and Eliza Hall Institute and La Trobe University (the latter two in Australia) had questioned the usefulness and activity of several stapled Bim BH3 peptides. The original researchers (Walensky et al.) had then fired back strongly, pointing out that the criticisms seemed misdirected and directing the authors back to what they thought had been well-documented principles of working with such species.

Now the WEHI/Genentech/La Trobe group (Okamoto et al.) has responded, and it doesn't look like things are going to calm down any time soon. They'd made a lot of the 20-mer stapled peptide being inactive in cells, while the reply had been that yes, that's true, as you might have learned from reading the original papers again - it was the 21-mer that was active in cells. Okamoto and co-workers now say that they've confirmed this, but only in some cell lines - there are others for which the 21-mer is still inactive. What's more, they say that a modified but un-stapled 21-mer is just as active as the closed peptide, which suggests that the stapling might not be the key factor at all.

There's another glove thrown down (again). The earlier Genentech/WEHI/La Trobe paper had shown that the 20-mer had impaired binding to a range of Bcl target proteins. Walensky's team had replied that the 20-mer had been designed to have lower affinity, thus the poor binding results. But this new paper says that the 21-mer shows similarly poor binding behavior, so that can't be right, either.

This is a really short communication, and you get the impression that it was fired off as quickly as possible after the Walensky et al. rebuttal. There will, no doubt, be a reply. One aspect of it, I'm guessing, will be that contention about the unstapled peptide activity. I believe that the Walensky side of the argument have already shown that these substituted-but-unstapled peptides can show enhanced activity, probably due to cranking up their alpha-helical character (just not all the way to stapling them into that form). We shall see.

And this blowup reflects a lot of earlier dispute about Bcl, BAX/BAK peptides, and apoptosis in general. The WEHI group and others have been arguing out the details of these interactions in print for years, and this may be just another battlefield.

Comments (8) + TrackBacks (0) | Category: Chemical Biology | Drug Assays


1. entropyGain on February 24, 2014 11:03 AM writes...

This is very healthy. We actually need more replication and challenging of claims. Too much goes unchallenged in our game these days.

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2. Anonymous on February 24, 2014 12:27 PM writes...

If you look at the papers by Walensky and other scientists over the years, the stapled peptides bind their targets with higher affinity than standard peptides time and time again. For BIM BH3, this was shown very clearly in the Walensky Molecular Cell paper in 2006. So it’s not clear what the Genentech and WEHI scientists are actually doing, although Walensky uses fluorescence polarization solution binding assays and the others do binding on a solid support (plasmon resonance), which I guess could cause differences. The most important point seems to be that Walensky developed the stapled BIM BH3 peptides to study BAX binding, where the stapling really has a pronounced benefit. The Genentech and WEHI scientists again don't test binding of the BIM BH3 peptides to the BAX protein, which seems pretty disingenuous. In their reply, the Genentech and WEHI investigators also sweep under the rug another central point, which is now that they use the right stapled BIM peptide in leukemia cells, they actually reproduce the Walensky results!

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3. couplin rgnt on February 24, 2014 12:43 PM writes...

the purity of peptides is usually.......

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4. Curious Wavefunction on February 24, 2014 2:57 PM writes...

Walensky and Bird have a nice review on stapled peptides in the "Just Accepted" section of J. Med. Chem. right now.

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5. Anonymous on February 24, 2014 3:02 PM writes...

FP is an indirect and dangerous method, can easily overestimate the affinity. I am not working on stapled peptides and do not follow the literature closely so my question is whether anyone measured Kd by ITC ?

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6. chemlinker on February 24, 2014 4:52 PM writes...

Direct binding analysis with FP can be very accurate and has the benefit of not biasing the binding setup to a particular protein direction, which solid phase approaches do...pre- organizes the protein with the added issue of non-specific sticking to surfaces. Don't see ITC reported for these, but it could be that the high concentrations required for protein and ligand would make the analysis difficult. Most binding methods have imperfections but any one method should be good enough to evaluate comparative binding activities.

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7. sgcox on February 24, 2014 5:46 PM writes...

Sorry, but I have to disagree about "direct" FP. For example, titration of the labeled peptide with a protein tells nothing about the stoichiometry and hence the affinity to any single binding site. It is always possible that your labeled peptide (compound)is simply sticky and each protein molecule sucks up more than one peptide (compound), making the apparent EC50 far better than Kd to the supposed binding site. Unless confirmed by orthogonal methods, any number is just a hypotheses.

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8. Bioorganic Chemist on February 25, 2014 11:48 AM writes...

Direct FP can be easily confirmed by a competition FP experiment with the unlabeled peptide - the Kd values damn well better be the same for the labeled and unlabeled peptide. Similarly, anyone doing proper FP knows to replicate the experiment at different concentrations to provide some evidence that one is not seeing aggregation - again the values obtained had better be the same. FP methods have the specific advantage of being able to be used at much lower concentrations than typical for ITC methods - working at concentrations of both binding partners around (or below) the Kd is absolutely critical for accurate Kd measurement. I laugh (and then cry) any time I see ITC measurements of low-mid-nM Kd when the experiments are done at low-mid-micromolar concentrations. ITC is lovely for confirmation of results, but is fraught with its own set of perils. SPR in theory can address the advantages of both (ability to work at low concentrations and conduct titrations with detection of a direct interaction), but so much of SPR depends on the method of attachment to the surface and the surface composition. (Also, the Kd by SPR should be done by titration, not by koff/kon (though that is lovely confirmation).) I've had way too many anomalous results with SPR to trust it without thorough validation by a competing technique. Though perhaps that's the issue here - any one experiment needs to be followed up with appropriate controls that address the limitations and potential biases of the approach.

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