Return to Flatland

Whoever first referred to Economics as ‘The Dismal Science’ had clearly never read an article on ‘3Dness’ in drug discovery.  My own experience reading articles on this topic is a sensation of having my life force slowly sucked out (I even suggested that reviewing the '3Dness' literature might be considered as an appropriate penance when I recently confessed my sins at St Gallen Cathedral) and the subject of Confession reminds me of a song that the late great Tom Lehrer sang about the Second Vatican Council.

In this post I review the CNM2025 study (Return to Flatland) which examines the heavily-cited LBH2009 study (Escape from Flatland: Increasing Saturation as an Approach to Improving Clinical Success).This also is a good point to mention a Journal of Medicinal Chemistry Editorial (Property-Based Drug Design Merits a Nobel Prize) that I reviewed in a 30-Jul-2024 post. The CNM2025 study, which has already been reviewed by Dan and Ash, opens with: 

The year is 2009, Barack Obama has just been inaugurated and both Lady Gaga and The Black Eyed Peas are at the height of their popularity

This couldn’t help but remind me of the “WORLD WAR 2 BOMBER FOUND ON MOON” headline that appeared on the front page of the Sunday Sport twenty-one years before the publication of LBH2009 (it was was accompanied by a photo of a B-17 in a lunar crater). A few weeks later the headline was “WORLD WAR 2 BOMBER FOUND ON MOON VANISHES” (this time accompanied by a photo of the now empty lunar crater).

I’ll start my review of CNM2025 by quoting from it and, as is usual for posts here at Molecular Design, quoted text is indented with any comments by me italicized in red and enclosed in square brackets. 

The hypothesis was attractive, and the data clearly showed the relationship between Fsp³ and clinical progression with pairwise significance P < 0.001. [This statement is inaccurate and Figure 3 of the LBH2009 study shows statistically significant differences at this level between (a) discovery and phase 2 compounds (b) phase 1 and phase 3 compounds (c) phase 2 compounds & drugs.  The authors of LBH2009 state: “The change in average Fsp³ was statistically significant between adjacent stages in only one case (phase 1 to phase 2)” but they neither show this in Figure 3 of their article nor do they report a P-value for the statistical significance of the mean difference in Fsp³ between phase 1 and phase 2 compounds.] The statistics seemed compelling, though the effect size was modest — an increase in average Fsp³ of 0.09 between sets of phase I and approved drugs equates to a difference of around two additional sp³ carbons per drug molecule only. [The authors of LBH2009 did not actually report this difference to be statistically significant so it is unclear why the authors of CNM2025 have stated that the “statistics seemed compelling”.]

The LBH2009 study is effectively a call to think beyond aromatic rings in drug design and my view is that there are considerable benefits in doing so even though I consider the data analysis in the study to be shaky. Almost three decades ago I included a quinuclidine in the Zeneca fragment library for NMR screening and later at AstraZeneca I would actively search (with minimal success) for amides and heteroaryls derived from bicyclic amines. I see the advantages in looking beyond aromatic rings as stemming primarily from increased molecular diversity and a more controllable coverage of chemical space, and in KM2013 we wrote:

Molecular recognition considerations suggest a focus on achieving axial substitution in saturated rings with minimal steric footprint, for example by exploiting the anomeric effect or by substituting N-acylated cyclic amines at C2.

Although data analyses (for example, see HY2010) presented in support of the belief that aromatic rings adversely affect aqueous solubility are typically underwhelming I consider the suggestion to be plausible and suggested in K2022 that deleterious effects of aromatic rings are more likely to be due to their potential for making molecular interactions than to their planarity. That said, I should also point out that the analysis of the relationship between aqueous solubility and Fsp³ presented in Figure 5 of LBH2009 is a textbook example of correlation inflation (see Fig. 5 in KM2013) and I suspect that if a team had submitted this analysis at Statistiques Sans Frontières the judges would have either awarded “nul points” or come to the conclusion that the team had played its joker. Given the Lady Gaga reference in CNM2025 I couldn't resist linking this Peter Gabriel song which includes the lyrics "Adolf builds a bonfire, Enrico plays with it" even though I have absolutely no idea what the the lyrics actually mean.

While the analysis of the relationship between aqueous solubility presented in Figure 5 of LBH2009 does endow the study with what I’ll politely call a whiff of the pasture it’s not directly related to the analysis of clinical progression presented in the study. Let’s take a look at Figure 3 in LBH2009 which shows mean Fsp³ values for compounds in discovery, at the three phases of clinical development, and approved drugs. As an aside this analysis would fall foul of current Journal of Medicinal Chemistry author guidelines (see link; accessed 05-Aug-2025) which clearly mandate that “If average values are reported from computational analysis, their variance must be documented”.  As mentioned earlier in this post Figure 3 in LBH2009 shows statistically significant (P value < 0.001) differences between (a) discovery and phase 2 compounds (b) phase 1 and phase 3 compounds (c) phase 2 compounds & drugs. It’s also worth stressing that Figure 3 in LBH2009 does not show statistically significant differences in Fsp³ for any of the clinical development transitions (phase 1 to phase 2; phase 2 to phase 3; phase 3 to approved drug). Figure 3 of in LBH2009 shows 591 phase 2 compounds but only 376 phase 1 compounds, raising questions about the numbers of compounds that have been in clinical development without being recorded in the database.

I think that there are some problems with how the authors of the LBH2009 study have analysed the relationship between Fsp³ and progression through the stages of clinical development.  If charged with analysing this data I would focus on the three clinical development transitions (phase 1 to phase 2; phase 2 to phase 3; phase 3 to approved drug) and wouldn’t waste time on comparisons between discovery compounds and clinical compounds. If analysing the relationship between Fsp³ and the progression from phase 1 to phase 2, I would partition the set of phase 1 compounds into a ‘YES’ subset of compounds that had progressed to phase 2 and a ‘NO’ subset of compounds that had not progressed to phase 2. I would certainly be taking a close  look at distributions of Fsp³ values (some approaches to assessing statistical significance are based on the assumption of Normally-distributed data values) and I’d also be thinking about assessing effect size in addition to statistical significance. However, the problems with the LBH2009 analysis are more fundamental than non-Normal distributions of Fsp³ values.

The authors of LBH2009 assess the progression from phase 1 to phase 2 by comparing the mean Fsp³ value for the phase 1 compounds with the mean Fsp³ value for phase 2 compounds. The problem is that the Fsp³ values for the YES compounds (that have progressed from phase 1 to phase 2) are present in both the data sets for which comparisons are being made. This means that the observed differences in mean Fsp³ values will reflect both the difference between YES and NO compounds (relevant to relationship between Fsp³ and progression from phase 1 to phase 2) and the relative numbers of YES and NO compounds in the phase 1 data (not relevant to relationship between Fsp³ and progression from phase 1 to phase 2). Analysing the data in the way that the authors of LBH2009 have done effectively adds noise to the signal and it’s possible that they would have observed more statistically significant differences in mean Fsp³ values had they analysed the data in a more appropriate manner.

This is an appropriate point at which to discuss correlation in the context of studies such as LBH2009 and CNM2025. It’s actually well known (see L2013) that that Fsp³ values for chemical structures tend to be greater when amine nitrogen atoms are present (this does not invalidate the observed trends in the data but has big implications for how you interpret these trends). There is, however, a much bigger issue which is that correlation does not imply causation. Let’s suppose that you’ve just joined a drug discovery team as they are preparing to select a clinical candidate (I concede that this is most improbable scenario but it does illustrate a point). The team have an excellent understanding of the structure-activity relationship (SAR) and have successfully addressed a number of issues during the lead optimization process (the chemical structures of the compounds have been quite literally shaped by the problems that the team members have solved). Now consider the likely reaction of the team members to a suggestion that probability of success in the clinic would increase if the chemical structure of the best compound were modified so as to increase its Fsp³ value. My view is that the team might think that the person making such a suggestion had just stepped off the shuttle from Planet Tharg (an alien from this planet used to make occasional Sunday Sport  appearances). I see the trends in data observed by the authors of LBH2009 as effects rather than causes (the vanishing B-17 was never there in the first place).

Let’s return to the CNM2025 study and its authors state:

Using data from the Cortellis Drug Discovery Intelligence database, we repeated an analysis similar to that of Lovering et al. to assess Fsp³ in drugs approved post-2009 and those in active clinical development as of mid-2024 (Fig. 1). [I would challenge the claim that the analysis presented in CNM2025 is similar to that presented in LBH2009. The supplementary material for CNM2025 indicates that the data summarised in Fig. 1b correspond to the period 2012 through 2024 (it is not clear whether the database has been updated to account for compounds that have fallen out of active development during this period. As is the case for Figure 3 in LBH2009, Fig.1b in CNM2025 shows more phase 2 compounds (816) than phase 1 compounds (421), raising similar questions about the numbers of compounds that have been in clinical development without being recorded in the database. I thank fellow blogger  Dan Erlanson for suggesting that I examine the supplemental information for CNM2025.] Although our methods used contemporary data sources different to Lovering et al., we obtained comparable Fsp³ data for approved drugs prior to 2009. More recently however, the picture appears to have changed with approvals shifting to lower Fsp³ drugs (Fig. 1a). Similarly, when looking at drugs currently in clinical development (Fig. 1b), there appeared to be no clear relationship between highest phase reached and Fsp³, suggesting the key conclusion noted by Lovering et al. has not persisted. In all data sets, exemplars with Fsp³ = 0 as well as Fsp³ = 1 are extensively seen. [It is necessary to account for the number of hypotheses have been tested for statistical significance when quoting P-values (see R2016 and VM2018).]

Fig. 1a in CNM2025 shows the time-dependence of Fsp³ distributions for approved drugs according to approval date and I remain unconvinced of the value of analysis like this (on first encountering analysis of time-dependence of drug properties a quarter of a century ago I recall being left with the distinct impression that some senior medicinal chemists where I worked had a bit too much time on their hands). However, it is immaterial whether or not you are as underwhelmed as I am by time-dependence of drug properties because no such analysis is actually reported in LBH2009 and this is one reason that I challenge the claim by made by the authors of CNM2025 that they “repeated an analysis similar to that of Lovering et al. to assess Fsp³ in drugs approved post-2009 and those in active clinical development as of mid-2024”.  

Now let’s take a look at Fig. 1b in CNM2025 and this should be compared with Figure 3 in LBH2009. In some ways the former is an improvement on the latter since the violin plots show the distributions of Fsp³ values for each group of compounds and, as mentioned earlier in the post, I don’t think that it makes any sense to include discovery compounds in analysis like this (as the authors of LBH2009 did). Although these two figures look superficially similar they are actually very different and, given that the authors of CNM2025 only included "compounds in clinical trials as of mid-2024" in their study, I would argue that their study does not properly examine the link between Fsp³ and clinical progression. I agree that the difference between mean Fsp³ values for drugs approved up to 2009 and for drugs approved after 2009 is statistically significant. What is not clear from the analysis summarized in Fig. 1b in CNM2025 is whether the lower Fsp³ values of drugs that were approved after 2009 reflect smaller increases in Fsp³ over the course of clinical development (the B-17 has disappeared from the lunar crater) or lower Fsp³ values for compounds entering clinical development (the B-17 is still in the lunar crater). I think it's possible to address this question but you would need to analyse the data a lot more carefully than the authors of CNM2025 appear to have done. For example, you might examine the time-dependencies of mean Fsp³ values for compounds evaluated in phase 1 and the corresponding mean Fsp³ values for compounds that progressed or failed to progress to phase 2. While I consider more careful analysis of progression to be feasible I see little or no value from the perspective of real world drug discovery in actually performing the analysis more carefully.

This is a good point at which to wrap up and, unless the the trends in the data can shown to reflect causation, the debate can be described as bald men fighting over a comb (as one who is follicly challenged I always find it painful to use this phrase). I see variation in drug properties with time as an effect rather than a cause and Forrest Gump would have been well aware of this fifteen years before the publication of LBH2019 when he famously observed that "shit happens". One point on which the CNM2025 authors and I do appear to agree is that there is not currently a B-17 in a lunar crater. Where we appear to differ is that they seem to be suggesting this was because it has vanished while I never believed that it was ever there in the first place. I’ll let the late great Dave Allen have the last word.

Natural Intelligence?

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My pulse will be quickenin'

With each drop of strychnine

We feed to a pigeon

It just takes a smidgin

To poison a pigeon in the park

Tom Lehrer, Poisoning Pigeons in the Park | video

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I’ll be reviewing the H2024 study (Occurrence of “Natural Selection in Successful Small Molecule Drug Discovery) in this post. Derek has already posted on the H2024 study which has been included in the BL2024 Virtual Special Issue on natural products (NPs) in medicinal chemistry. I'll also mention reviews here at Molecular Design of the the related studies (4) (see post) and (24) (see post). As is usual for Molecular Design reviews of literature I have used the same reference numbers that were used in H2024 and quoted text is indented with any comments by me in square brackets and italicised in red. Given the serious concerns I have about H2024 this is going to be a long post and there are a couple of disclaimers that I need to make before starting the review:

1. I regard identification and biological characterisation of NPs as vital scientific activities that should be generously funded and Derek puts it very well in his recent post ("When you see specific and complex small molecules that living creatures are going to the metabolic trouble to prepare, there are surely survival-linked functions behind them."). In particular, I see it as important that NPs be screened in diverse phenotypic assays and here’s a link to the Chemical Probes Portal. While my criticisms of H2024 are certainly serious it would be grossly inaccurate to take these criticisms as indicative of an anti-NP position.
2. Automation of workflows (N2017) and generation of datasets from databases such as ChEMBL are far from trivial and (33), which highlights some of the challenges faced by researchers in this area, was the subject of a recent post at Molecular Design. I consider method development in this area to be an important cheminformatic activity that should be adequately supported. It must also be stressed that the design, building and updating of databases such as ChEMBL (G2012 | B2014 | P2015 | G2017 | 23) are vital scientific activities that should be generously funded (had it not been of the vision and foresight of the creators of the PDB over half a century ago it is improbable that the 2024 Chemistry Nobel Prize would have been awarded for “computational protein design” and “protein structure prediction”). While my criticisms of H2024 are certainly serious it would be grossly inaccurate to take these as criticisms of the automated dataset generation described in the study (and recently published in H2024b) or of the contributions by a number of individuals that have made ChEMBL an invaluable resource for drug discovery scientists and chemical biologists.

Hampi, November 2013

Having made the disclaimers, I’ll open my review of H2024 with some general observations. First, I do not consider that H2024 presents any insights of practical value to medicinal chemists nor do I consider the analyses presented in the study to support the assertion that “there is untapped potential awaiting exploitation, by applying nature’s building blocks─’natural intelligence’─to drug design” (in my view the use of the term “natural intelligence” does rather endow the study with what I’ll politely refer to as a distinctly pastoral odour). Second, the results of the analyses presented in H2024 do not demonstrate any tangible benefits from the drug design perspective of incorporating structural features that have been anointed as 'natural' by the authors (my view is that it would be extremely difficult to design data analyses to address the relevant questions in an objective manner). Third, the authors of H2024 present a ‘scaffold-centric’ view of NPs in which the naturalness of NPs is due to cyclic substructures present within their chemical (2D) structures (it is almost as if these 'natural' substructures are considered to be infused with 'vital force') and I would question whether this is a realistic view from the molecular recognition and physicochemical perspectives.  Fourth, the meaning of what the authors of H2024 are calling 'enrichment' of pseudo-NPs (PNPs) in clinical compounds is unclear and, in any case, the 'enrichment' values do seem rather low (never more than twofold) when you consider the numbers of compounds that successful discovery project teams typically have to synthesize in order to deliver a drug that gets to market.

It's not clear (at least to me) what the authors of H2024 mean by ‘natural selection’ and at times their view of natural selection appears to be closer to Lysenkoism than Darwinism. For example, they assert in the conclusions section of H2024 that “NP structural motifs are provided predesigned by nature, constructed for biological purposes as a result of 4 billion years of evolution.” Design actually has no place in natural selection and perhaps the authors are thinking of 'Intelligent Design' which is a doctrine with many adherents in the Creationist community.  While I don’t dispute that the chemical structures of many clinical compounds contain substructures that are also found in the chemical structures of NPs, I think that it would be extremely difficult to objectively compare different explanations for the observations (it's worth remembering that correlation does not imply causation). The explanation favoured by the authors of H2024 is that compounds assembled from Nature’s building blocks are ‘better’ and a stated aim of the study is “to seek further support for the existence of ‘natural selection’ in drug discovery” (this video will give readers an idea of what the late great Dave Allen might have made of this). In my view the data analyses presented in H2024 are not actually based on statistics and are therefore unfit for the purpose of testing hypotheses. Put another way, if you're going to use data analysis to look for something then it would be a good idea to use methods capable of telling you that you that haven't found what you were looking for.    

 

The data analyses in H2024 are largely based on quantities (PNP_Status | Frag_coverage_Murcko | NP-likeness) that are calculated from the chemical (2D) structures of compounds.  However, the authors do not state which software was used to perform the calculations and, had I been a reviewer, I would have drawn their attention to the following directive in the Data Requirements section in the J Med Chem Author Guidelines (accessed 27-Dec-2024):

9. Software. Software used as a part of computer-aided drug design should be readily available from reliable sources, and the authors should specify where the software can be obtained.

As was the case for my review of (24) I see much of the analysis in H2024 as relatively harmless “stamp collecting” (in contrast, as discussed in KM2013, I consider presentations and analyses of data that exaggerate trend strength, such as those used in the HMO2006, LS2007, LBH2009, HY2010 and TY2020 studies to be anything but harmless). The analyses that I’ll be examining in this post are of comparisons between clinical compounds and reference compounds although I'll comment in general terms on the analyses of time-dependencies of characteristics of clinical compounds. My general criticism of H2024 is not that the analyses presented by its authors are necessarily invalid but that they fail to provide any useful insight and I’ll share an insightful observation by Manfred Eigen (1927-2019):

A theory has only the alternative of being right or wrong. A model has a third possibility: it may be right, but irrelevant.

I first encountered analyses of time-dependencies of drug properties about two decades ago and rapidly came to the conclusion that some senior medicinal chemists where I worked had a bit too much time on their hands.  The fundamental flaw in the interpretation of these analyses is that time-dependencies of the properties of drugs and other clinical compounds are presented as causes rather than effects and it has never been clear how medicinal chemists working on drug discovery projects in the real world should use the results from such analyses. The authors claim that “changes to drug properties over time are significant” and I would challenge them to present even a single example of such analysis being used to meaningfully inform decision-making in a drug discovery project. It must be stressed that my criticism of analyses of time-dependency of the properties of drugs and other clinical compounds is simply that they don't provide useful insights and not that the analyses are necessarily invalid. That said, I do have general concerns about how time-dependencies are compared when some of the properties are expressed as logarithms and some are not. As reviewer I would have recommended that the vertical axis of the plot in the graphical abstract be drawn from 0% to 100% rather than from 30% to ~67%.

As is the case for analyses of time-dependency, my criticism of analyses of the differences between clinical compounds and reference compounds is that they don’t provide useful insight and there is no suggestion that the analyses are necessarily invalid. Before looking at the analyses presented in H2024 I’ll quote from the abstract of (24) because this will give you an idea of what I mean by analyses not providing useful insight:

Drugs are differentiated from target comparators by higher potency, ligand efficiency (LE), lipophilic ligand efficiency (LLE), and lower carboaromaticity.

As I noted in this post (this focused principally on the invalidity of the LE metric as discussed in NoLE) reporting that an analysis has shown drugs to be differentiated by potency from target comparators does seem to be stating the obvious and, given how LE and LLE are defined, it is perhaps not the most penetrating of insights to observe that values of these efficiency metrics tend to be greater for drugs than for comparator compounds. While the observation of lower carboaromaticity of drugs relative to comparator compounds is non-obvious, it does not constitute information that can be used for medicinal chemistry decision-making in specific discovery projects (as we noted in KM2013 carboaromaticity and lipophilicity can both be reduced simply by replacing a benzene ring with benzoquinone).

Let’s take a look at how this type of analysis is used in H2024. The authors of H2024 note that “comparing Figure 3a,b shows a clear ‘enrichment’ of PNPs in clinical compounds versus reference compounds in the post-2008 period” and two of these authors, writing in (17), assert that “PNPs have increasingly been explored in recent drug discovery programs, and are strongly enriched in clinical compounds”.  What the authors of H2024 are calling 'enrichment' is rather different to the enrichment in structural features that results from high-throughput screening (HTS) and it’s important to understand the difference. Let’s suppose that we’ve screened a library of compounds of which 1% are pyrimidines and 1% are pyrazines and we find that 10% of the hits are pyrimidines and 0.1% are pyrazines (to simplify things you can assume there is no compound in the library with a pyrimidine and a pyrazine in its chemical structure). In this case we would conclude that the process of screening has resulted in a tenfold enrichment for pyrimidines and a tenfold impoverishment for pyrazines. Now let's create a 'selected azines' category by combining the pyrimidines and pyrazines which as a structural class comprise 2% of the screening library compounds but 10.1% of the hits. What I'm getting at here is that enrichment of an more inclusive structural class such as 'selected azines' (or PNPs) does not imply that each and every one of the structural classes covered by the inclusive structural class definition will also be enriched.

Now let’s take a look at how the 'enrichment' of PNPs in clinical compounds is assessed in H2024. First, a set of reference compounds is generated for each clinical compound (this is discussed in detail in H2024b) and the sets of reference compounds are combined. 'Enrichment' is then assessed by comparing the fraction of clinical compounds that are PNPs with the fraction of compounds in the combined reference sets that are PNPs. When we assess enrichment of chemotypes in HTS the hits are all selected (by the screening process) from the same reference pool of compounds. In contrast, each clinical compound in the H2024 analysis is associated with a different reference set of compounds (from the perspective of data analysis combining reference sets defined in this manner gratuitously throws information away). As a reviewer I would have pressed the authors to enlighten readers as to how they should interpret the proportions of PNPs in the reference sets for individual compounds.

It's worth thinking about what the reference compound set might look like for a clinical compound that is a PNP. The proportion of PNPs in the reference set will generally be influenced by factors such as availability of data, the ‘rarity’ of the structural features of the drug and the ‘tightness’ of the structure-activity relationship (SAR).  A more permissive definition of ‘activity’ would generally be expected to make SAR appear to be less ‘tight’ (or ‘looser’ if you prefer). Compounds were defined as ‘active’ for the analysis on the basis of a recorded pChEMBL value against one of the clinical compound’s targets (as a reviewer I’d have suggested that the authors define the term ‘pChEMBL’) which means that a compound might have been selected for inclusion in a reference set on the basis of an IC₅₀ value of 100 μM.

Let’s define 'enrichment' by dividing the fraction of the clinical compounds that are PNPs by the fraction of reference compounds that are PNPs. When we select a reference set for a clinical compound that is a PNP then it’s extremely unlikely that every single compound in the reference set will also be a PNP (especially if we’re accepting compounds with IC₅₀ values 100 μM as ‘active’) and it’s even less likely that every single compound in the combined reference sets will be a PNP. This means that we should generally expect the clinical compounds that are PNPs to be ‘enriched’ in PNPs when compared with their combined reference sets. We can apply exactly the same logic to conclude that we should expect that the combined reference sets for the clinical compounds that are not PNPs  (under this scenario we would conclude that the set of clinical compounds that are not PNPs are infinitely impoverished in PNPs when compared with their combined reference sets). This means that we should expect that the 'enrichment' of PNPs in the clinical compound set in comparison with their combined reference sets will increase with the fraction of clinical compounds that are PNPs.

Let’s take another look at the plot in the graphical abstract which shows the fractions of clinical compounds and reference compounds that are PNPs as a function of time. Notice how the lines tend to be furthest apart when the fraction of clinical compounds that are PNPs is relatively high. As a reviewer, I would have required that the authors examine the correlation between the logarithm of the fraction of clinical compounds and the logarithm of the enrichment (a relatively strong correlation would indicate that the information added by the combined reference sets is minimal). The 'enrichments' calculated from the plot in the graphical abstract are underwhelming (the highest degree of enrichment is the 2014 value of just over 1.5-fold and this value seems very low when you consider the numbers of compounds that successful discovery project teams typically need to synthesize in order to get drugs approved).  From 2011 the fraction of clinical compounds that are PNPs exceeds 50% but I wouldn't consider it accurate to use the term "strongly enriched" (17) because the fraction of reference compounds that are PNPs is 40% or greater for this time period (plotting the vertical axis in the graphical abstract from 30% to ~67%  creates the illusion that the 'enrichment' is greater than it actually is).

I do have a number of other gripes about the data analysis in H2024 but I do also need to take a look at PNPs and the following assertion by the authors is an appropriate point at which to start this discussion:

The PNP concept has been validated by its appearance in the literature (16,17) and by the design of several new classes of biologically active compounds. (18,19) [As a reviewer I would have pressed the authors to clearly articulate the “PNP concept” (just as I would have pressed the authors of this Editorial to clearly articulate the new principles that their nominees for the Nobel Prize in Physiology or Medicine had introduced).  My view is that it is verging on megalomania to claim that a concept “has been validated by its appearance in the literature” and I don’t consider (18) to support the claim for “design of several new classes of biologically active compounds”. To support such a claim, one would ideally need to demonstrate that screening of libraries of compounds designed as PNPs resulted in the discovery of viable lead series against a range of therapeutic targets. At absolute minimum, one would need to show that libraries of compounds designed as PNPs exhibited exploitable activity across a range of target-related assays (although interesting, the results from the “cell painting assay” would not by themselves support a claim for “design of several new classes of biologically active compounds”). I should also mention that some in the compound quality field (see B2023 and my review of that article) interpret activity against multiple targets for a set of compounds based on a particular scaffold as evidence for pan-assay interference even when the individual compounds don’t themselves exhibit frequent-hitter behaviour. I don't have access to (19) and am therefore unable to assess the degree to which that article supports the authors claim for “design of several new classes of biologically active compounds”.]

The PNP status of a compound is determined by how “NP library fragments” (these are cyclic substructures extracted from the chemical structures of compounds in an NP-focussed screening library that had been generated over a decade ago for fragment-based drug discovery) are combined in its chemical structure.

 

PNP_Status. Compounds were assigned to one of four categories according to their NP fragment combination graphs. (16,17) The NP library fragments used for this purpose are Murcko scaffolds (26) [It would be actually more appropriate to refer to these as ‘Bemis scaffolds’ in order to properly recognize the corresponding author of this article.] (the core structures containing all rings without substituents except for double bonds, n = 1673) derived (16) from a representative set of 2000 NP fragment clusters. (15) [I see this approach as unlikely to capture all the relevant cyclic substructures present in NPs.  My view is that it would have been better to first extract the relevant cyclic substructures from the chemical structures of all NPs for which this information is available, and then do the selection and filtering in one or more subsequent steps. The other advantage of doing things this way is that you’ll get a better assessment of the frequencies with which the different cyclic substructures occur in the chemical structures of NPs.]  Because of their ubiquitous appearances in NPs, the phenyl ring and glucose moieties were specifically excluded as fragments. (16) [I would expect exclusion of the benzene ring (I consider ‘benzene ring’ more correct than ‘phenyl ring’ in this context) as a fragment to result is a significant reduction in number of the number of compounds that are considered to be PNPs (and, by implication, the ‘enrichment’ associated with membership of the PNP class).  Even though the benzene ring has been excluded for the purpose of assigning PNP status it should still be considered to be one of Nature’s building blocks.]

As I mentioned earlier in the post, the view of NPs presented in H2024 is ‘scaffold-centric’ and I would question how realistic this view is given that non-scaffold atoms at the periphery of a molecular structure will generally be more exposed to targets (and anti-targets) than scaffold atoms at the core of the molecular structure. What I’m getting at here is that it is far from clear how much of a compound’s pharmacological activity can be attributed to the presence of individual substructural features in the chemical structure of the compound (modifying a point made in NoLE, I would argue that the contribution of a structural feature to the binding affinity of a compound is not actually an experimental observable). This is one reason that unless matched molecular pairs are available it would not generally be possible to demonstrate the superiority of one structural feature over another in an objective manner.

Something that you need to pay very close attention to when extracting substructures from chemical structures of compounds is the ‘environment’ of the substructure (I prefer to use the term ‘substructural context’). For example, two piperidine rings linked through nitrogen look very different from the perspective of a therapeutic target protein depending on whether the link is a carbonyl carbon or a tetrahedral carbon (most medicinal chemists will be aware that the protonation states differ but there are also subtle, although still significant, differences in the shape of the piperidine ring in the two substructures). You also need to be aware that fusing rings can have profound effects on physicochemical characteristics and I would consider it a bad idea to extract monocyclic substructures from fused or bicyclic ring systems.

There are some things that don't look quite right and I would have flagged these up if I’d been reviewing the manuscript. Let’s take a look at the first entry (Sotorasib) in Table 1 and you can see that the oxygen of the 2-pyrimidone substructure is coloured lilac indicating that this substructure can be found in the chemical structures of one or more NPs (I would still challenge the view that the result of fusing 2-pyrimidone with pyridine should be considered 'natural' on the basis that the heterocycles from which it is derived from are both found in chemical structures of NPs). Now take a look the second entry (Dolutegravir) in Table 1 and you'll notice that the oxygen in the 4-pyridone substructure is not coloured green. This implies that 4-pyridone does not occur in the chemical structure of any NP and, in the absence of  information, I can only assume that it has been anointed as 'natural' because of its structural analogy with pyridine (while there is a nitrogen atom and five trigonal carbon atoms in each substructure the molecular recognition characteristics of the two substructures differ far too much for them to be regarded as equivalent from the perspective of assigning PNP status). Six of the substructures in Figure 5 appear to be in unstable tautomeric forms (first, fifth, ninth, twelfth entries in line 2 | seventh entry in line 3 | first entry in line 5).   

I'll conclude my review of  H2024 by commenting on claims made by the authors:

This is further evidence that the three NP metrics can be considered as independent measures of clinical compound quality. [I would consider the claim that any of these “NP metrics” can be considered as a measure of“clinical compound quality” to be wildly extravagant (the authors haven't even stated how "clinical compound quality" is defined yet they claim to be able to measure it). I would argue that compound quality cannot be meaningfully compared for clinical compounds that have been developed for different diseases or disorders. Describing a compound as 'clinical' implies that a large body of measured data has actually been generated for it and the authors of H2024 might find it instructive to ask themselves why they think a simple metric calculated from the chemical structure of the compound would be of interest to a project team with access to this large of body of measured data One criticism that I make of drug discovery metrics is that they trivialize drug discovery and we noted in KM2013: “Given that drug discovery would appear to be anything but simple, the simplicity of a drug-likeness model could actually be taken as evidence for its irrelevance to drug discovery.” ]

The overall results are supportive of the occurrence of “natural selection” being associated with many successful drug discovery campaigns. [My view is that the authors of H2024 have not clearly articulated what they mean by“natural selection” in the context of this study.]  It has been proposed that NP-likeness assists drug distribution by membrane transporters, (21) [The author of (20c) asserts "Over the years, my colleagues and I have come to realise that the likelihood of pharmaceutical drugs being able to diffuse through whatever unhindered phospholipid bilayer may exist in intact biological membranes in vivo is vanishingly low" and, by implication, that entry of the vast majority of drugs into cells is transporter mediated. I keep an open mind on this issue although I note that what is touted by some as a universal phenomenon does seem to have been remarkably difficult to observe directly by experiment. The difficulties caused by active efflux are widely recognized by drug discovery scientists and it may be instructive for the authors of H2024 to consider how an experienced medicinal chemist working in the CNS area might view a suggestion that compounds should be made more like NPs to increase the likelihood of being transporter substrates.] and we further speculate that employing NP fragments may result in less attrition due to toxicity, a major cause of preclinical failure. (55) [This does seem to be grasping at straws. The focus of the cited article is actually clinical failure and not preclinical failure.]

There is untapped potential for further exploitation of currently used and unused NP fragments, especially in fragment combinations and the design of PNPs, without the need to resort to chemically diverse ring systems and scaffolds. [This exemplifies what can be called the ‘Ro5 mentality’ (‘experts’ advising medicinal chemists to not explore but to focus on regions of chemical space that have been blessed by the ‘experts’). As I note in this blog post Ro5 (as it is stated) is not actually supported by data and in NoLE, I advise drug designers not to “automatically assume that conclusions drawn from analysis of large, structurally-diverse data sets are necessarily relevant to the specific drug design projects on which they are working.” An equally plausible 'explanation' for the observation that a high fraction of clinical compounds are PNPs is simply that medicinal chemists are working with what they're most familiar with (in this case the advice would be to look beyond Nature's building blocks for inspiration).] To exploit these opportunities, “NP awareness” needs to be added to the repertoire of medicinal chemists. [My view is that it would be more important for critical thinking to be added to the repertoire of medicinal chemists so they are better equipped to assess the extent to which conclusions and recommendations of studies like H2024 are actually supported by data.]

In short, applying nature’s building blocks─natural intelligence─to drug design can enhance the opportunities now offered by artificial intelligence. [In my view "natural intelligence" appears to be arm-waving that is neither natural nor intelligent.]  

This is a good point to wrap up and to also conclude blogging for the year. My new year wish is for a kinder, happier and more peaceful World in 2025 and I'll leave you with a photo of BB and Coco in the study here in Maraval. They had been helping me with this post before I unwisely decided to explain ligand efficiency to them. Let sleeping dogs lie I guess.

 

A Nobel for property-based drug design?

[This post was updated on 10-Aug-2025 to mention my review of CNM2025 (Return to Flatland) which  critically examines (35) (Escape from Flatland: Increasing Saturation as an Approach to Improving Clinical Success)] 

 

This post was updated on 04-Aug-2024. I thank Tim Ritchie (see RM2009 | RM2014) for bringing YG2003 (Prediction of Aqueous Solubility of Organic Compounds by Topological Descriptors) to my attention.]

"The problems of ADME are precisely those that determine success or failure of a drug in vivo. In vitro data can give a clearer picture of the receptor characteristics, but knowledge and control of ADME are also vital. A common trap in binding studies is that binding generally increases with lipophilicity, so that one may obtain extremely potent binding that is totally unattainable in vivo."

SH Unger (1987) Computer-Aided Drug Design in the Year 2000. 

Drug Information Journal 21:267-275 DOI

******************************************

In this post I’ll be reviewing an Editorial (Property-Based Drug Design Merits a Nobel Prize) that was recently published in J Med Chem. For me, the Editorial raises questions about the critical thinking skills of its authors and of the judgement of the J Med Chem Editors (I’m guessing that some of the courteous and cultured members of the Nobel Prize committee might regard it to be somewhat pushy, and possibly even uncouth, for journals to be publishing nominations for Nobel Prizes as editorials). My advice to anybody nominating individuals for a Nobel Prize is to be aware of an observation, usually attributed to Jocelyn Bell Burnett, that it’s better that people ask why you didn’t win a Nobel Prize than why you did. Where applicable, I've used the the same reference numbers that were used in the Editorial and I’ll start by reproducing the Nobel Prize proposal (as is usual in posts at Molecular Design, I’ve inserted some comments, italicized in red and enclosed in square brackets, into the quoted text):

We propose that a Nobel Prize in Physiology or Medicine should be awarded for property-based drug design, with Christopher A. Lipinski, Paul D. Leeson, and Frank Lovering as the proposed recipients for their development of “important principles for drug design” [I would describe what the proposed Nobel laureates have introduced as a rule, a metric and a molecular descriptor rather than principles.], principles that have contributed to the development of numerous approved drugs. [The authors do need to provide convincing evidence to support what appear to be some wildly extravagant claims. Specifically, the authors need to demonstrate that the rule, metric and molecular descriptor (which they describe as “principles”) were actually critical to the decision-making in projects that led to the development of numerous drugs.] While drug design previously focused primarily on optimizing potency, they introduced a more holistic approach based on the consideration of how fundamental molecular and physicochemical properties affect pharmaceutical, pharmacodynamic, pharmacokinetic, and safety properties. [My view is that none of proposed Nobel laureates even demonstrated a single convincing link between molecular and physicochemical properties, and pharmaceutical, pharmacodynamic, pharmacokinetic, and safety properties.] The development of the Rof5 by Christopher A. Lipinski in 1997 introduced a new principle for how molecular and physicochemical properties affect oral bioavailability. The development of LipE by Paul D. Leeson in 2007 introduced a new principle for how physicochemical properties impact potency, selectivity, and safety. Finally, the development of Fsp3 by Frank Lovering in 2009 introduced a new principle for how molecular shape affects pharmaceutical properties and developability.

Before examining the contributions of the three nominated individuals it's worth saying something about the objectives of drug design. First, a drug needs to be highly active against its target(s). Second, activity against anti-targets should be very low (ideally too low to even be measured). Third, as I note in 34, the exposure (concentration at the site of action) of the drug needs to be controllable (one challenge in drug design is that intracellular drug concentration can’t generally be measured in vivo and I recommend that all drug discovery scientists read SR2019). I see controlling exposure as the primary focus of property-based design and one fundamental challenge is that structural modifications that lead to increased engagement potential for the therapeutic target(s) frequently result in reduced controllability of exposure as well as increased engagement potential for anti-targets. I’ve tried to capture these points in the graphic shown below.

It's generally accepted that excessive lipophilicity and molecular size are risk factors in drug design and the “compound quality” (CQ) literature abounds with fire-and-brimstone sermons on the evils of "molecular obesity" (see H2011). Nevertheless, the relationships between these descriptors and properties such as binding affinity for anti-targets, permeability, aqueous solubility and metabolic lability are generally not quite as strong as is commonly believed (or claimed). When using trends in data to inform design it’s really important to know how strong the trends are because this tells you how much weight to give to the trends when making decisions. It’s not unknown in CQ studies for trends in data to be made to appear to be stronger than they actually are which endows the CQ field with what I’ll politely call a “whiff of the pasture” (the term “correlation inflation” has been used; see KM2013). Transformation of continuous data (IC₅₀ values) to categorical data (high | medium | low) prior to analysis should trigger a deafening cacophony of alarm bells as should any averaging of groups of continuous data values without showing the spread in the data values. Some examples of studies in which I consider the strengths of trends to have been exaggerated include 29, 35, HMO2016 and HY2010.

I think that one thing that everybody who actually works (or has worked) on drug discovery projects agrees on is that drug discovery is really difficult. My view is that, by focusing on Rof5, LipE and Fsp3, the Editorial actually trivializes the challenges faced by drug discovery scientists. Most drug design (as opposed to ligand design) takes place during lead optimization and lead optimization teams are typically addressing specific problems (for example, structural changes that result in increased potency also result in reduced aqueous solubility).  Lead optimization teams typically work with a lot of measured data (a significant component of drug design is efficient generation of data to enable decision-making) and a weak correlation between logP and aqueous solubility reported in the literature would be of no practical relevance when the lead optimization team is using aqueous solubility measurements for compounds in the structural series that they’re optimizing. It is common (see M2001 | G2008) for the simplicity of rules, guidelines and metrics to be touted and we noted in KM2013 that:   

Given that drug discovery would appear to be anything but simple, the simplicity of a drug-likeness model could actually be taken as evidence for its irrelevance to drug discovery.

Guidelines for successful drug discovery are often presented in terms of something good (or bad) being more likely to happen when the value of a calculated property such as Fsp3 exceeds a threshold. When using guidelines like these be aware that it’s actually very difficult to set these threshold values objectively and that the guidelines would have been stated in an identical manner had different threshold values been chosen to specify them. One difficulty with using guidelines like these is that the creators of the guidelines don’t usually say what they mean by “more likely” (millions of people book flights knowing that one is “more likely” to die in a plane crash if one takes a flight than if one doesn’t take a flight). A number of published guidelines (some of which have been referenced in the Editorial) claim that compounds that comply with the guidelines are more likely to be developable. However, giving weight to these claims would require that developability be defined in an objective manner that enables compounds with arbitrary molecular structures and differing biological activity to be meaningfully compared.   

I’ll examine the contributions of the three proposed laureates for the Nobel Prize in Physiology or Medicine following the order in the Editorial. Let's start with the first:

  

The development of the Rof5 by Christopher A. Lipinski in 1997 introduced a new principle for how molecular and physicochemical properties affect oral bioavailability. [As a reviewer of the manuscript I would have pressed the authors to explicitly state the new principle that their first nominee for the Nobel Prize for Physiology or Medicine had introduced 1997.]

My view is that the publication of the Rof5 (22) has certainly proven to be highly influential in that it made many drug discovery scientists aware of the need to take account of physicochemical properties, in particular lipophilicity, in drug design. What is less well-known, but possibly more important in my view, is that publication of the Rof5 sent a clear message to Pharma/Biotech management that high-throughput screening wasn’t going to be the panacea that many believed that it would be. However, I don't see the Rof5 as quite the epiphany that the authors of the Editorial would have us believe it to be. The quote with which I started this post was taken from an article that had been published ten years before 22 and the inverse nature of the relationship between aqueous solubility and lipophilicity was being discussed in the scientific literature (see YV1980) more than forty years ago. The NC1996 study is also worthy of mention because it was published more than a year before 22 and it makes the important point that optimal logP values are likely to vary with chemotype ("each congeneric series for a drug backbone usually demonstrates its own optimal log P").       

Questions can be raised about the data analysis presented in support of the Rof5 and readers may find it helpful to take a look at the S2019 study as well as my comments on the Rof5 in HBD3 and in this post. I would argue that the Rof5 does not have any practical value as a drug design tool and I would challenge the assertion made in the Editorial that the publication of 22 demonstrated how “molecular and physicochemical properties affect oral bioavailability”. One aspect of the analysis presented (22) in support of the Rof5 that isn't always fully appreciated is that the compounds for which the descriptors are calculated were all treated as having equivalent oral bioavailability (compounds were selected for the analysis on the basis of having been taken into phase 2 clinical trials at some point before the Rof5 had been published in 1997). This is one reason that it’s not credible to assert that the analysis demonstrates that these molecular and physicochemical properties are linked to bioavailability (it must be stressed that, like many, I do actually believe that excessive lipophilicity and molecular size are risk factors in drug design). I make the following point in a blog post (I’ve modified the original text very slightly for consistency with the Editorial):

The Rof5 is stated in terms of likelihood of poor absorption or permeation although no measured oral absorption or permeability data are given in 22 and the Rof5 should therefore be regarded as a statement of belief. I realise that to make such an assertion runs the risk of an appointment with the auto-da-fé and I stress that had the Rof5 been stated in terms of physicochemical and molecular property distributions I would not have made the assertion.

To see what I was getting at let’s take a look at how the Rof5 was stated in 22 (“The ‘rule of 5’ states that: poor absorption or permeation are more likely when…”). However, the analysis presented in support of the Rof5 was of the distribution of compounds in chemical space defined by molecular weight, logP and numbers of hydrogen bond donors and acceptors with no account being taken of variation in either absorption or permeation for the compounds. Analysis like this can be informative but you need to demonstrate that the chemical space is actually relevant to the phenomena of interest. One way that you can demonstrate that a chemical space is relevant is to build predictive models for the phenomena of interest using only the dimensions of the chemical space as descriptors. Alternatively you might observe meaningful differences between the distributions in the chemical space for compounds that have respectively passed and failed at at a particular stage in clinical development.  

So that’s all that I’ll be saying about Rof5 and it’s time to take a look at the contributions of the second proposed Nobel Laureate:

The development of LipE by Paul D. Leeson in 2007 introduced a new principle for how physicochemical properties impact potency, selectivity, and safety. [As a reviewer of the manuscript I would have pressed the authors to explicitly state the new principle that their second nominee for the Nobel Prize for Physiology or Medicine had introduced 2007.]

I'll start by saying that LipE is a simple mathematical formula and I suggest that one shouldn't be confusing simple mathematical formulae with principles when nominating people for Nobel Prizes. There are, however, other errors and these are not the kind of errors that you can afford to make when nominating people for Nobel Prizes. First, the term used in 29 is actually “ligand-lipophilicity efficiency” (LLE) although this appears to have mutated to “lipophilic ligand efficiency” (also LLE) by 2014 (see H2014). The term “LipE” was actually introduced by Pfizer scientists (see R2009) and it is significant that the more recent J2018 article defines LipE in terms of logD rather than logP (doing so means that you can make compounds more efficient simply by increasing extent of ionization and, as a drug design tactic, this is likely to end about as well as things did for the Sixth Army at Stalingrad).

The second (and more serious from the perspective of a Nobel nomination) error is that the metric had already been discussed, although not named, in the literature when 29 was published (I’m guessing that a suggestion that naming a metric merits a Nobel Prize for Physiology or Medicine might cause some members of the Nobel Prize committee to choke on their surströmming).  The L2006 book chapter, published fifteen months before 29, states:

Thus, to achieve compounds with a not too high log P while still retaining potency, the difference between the log potency and the log D can be utilised.

From the A2007 perspective which was published three months before 29: 

Lipophilicity is thought to be a driving force for binding to anti-targets such as the hERG ion channel and cytochrome p450 enzymes and potency can be scaled by lipophilicity by subtracting measured or calculated 1-octanol water partition coefficients from pIC₅₀.

It might be helpful to say something about efficiency metrics since LiPE (or LLE if you prefer) is an example of an efficiency metric. The idea behind efficiency metrics is to “normalize” a compound’s activity (typically quantified by potency or affinity) by the value of a risk factor such as lipophilicity or molecular size (for the masochists among you there’s an entire section in 34 on normalization of binding affinity). Ligand efficiency (LE) was introduced in 2004 (see H2004) and is generally regarded as the original efficiency metric although its creators do acknowledge the influence of the K1999 study. I’ve argued at length in 34 (Table 1 and Figure 1 in the article capture the essence of the argument) that LE is physically meaningless because perception of efficiency changes if you use a different concentration to define the standard state (by convention ΔG_binding values correspond to an arbitrary 1 M standard concentration) and there is no way to objectively select any particular value of the standard concentration for calculation of LE.  The problem doesn’t go away if you try to define ligand efficiency in terms of logarithmically expressed values of IC₅₀, K_i or K_d instead of ΔG_binding because these quantities still have to be divided by an arbitrary concentration value in order to be expressed as logarithms (see M2011).  My view is that LE shouldn't even be described as a metric and I sometimes appropriate a quote ("it's not even wrong") that is usually attributed to Pauli because those who advocate the use of LE in drug design are unable (or unwilling) to say what it measures.

The meaninglessness of LE stems from it being defined by scaling ΔG_binding by the design risk factor (molecular size). In contrast, LipE is defined by offsetting pIC₅₀ by the risk factor (logP) and can be interpreted (see 34) as the energetic cost of moving the ligand from octanol to its target binding site (this interpretation is only valid when the ligand binds in its neutral form and is predominantly neutral in the aqueous phase).  When considering lipophilicity in property-based design it is important to be aware that octanol is an arbitrary choice of solvent for measurement of partition coefficients and that the logP (or logD) calculated for a compound may differ significantly depending on the algorithm used for the calculations. That said, the hydrogen bond donors/acceptors and ionizable groups tend to be relatively conserved within structural series which means that the details of exactly how lipophilicity is quantified are likely to be less critical in lead optimization than for structurally-diverse sets of compounds.

When we use LipE we’re actually assuming that logP (or logD) is predictive of properties such as aqueous solubility, affinity for anti-targets and metabolic lability. That is why it’s not accurate to state that the introduction of LipE showed how “physicochemical properties impact potency, selectivity, and safety”.  In some published studies the focus is less on the LipE metric and more on what might be called the "lipophilic efficiency concept" (aim for top left corner of a plot of potency against lipophilicity). It is common to show reference lines of constant LipE to plots of potency against lipophilicity in this type of analysis and if you're doing this you really should be citing R2009 rather than 29. 

I'll finish the commentary on LipE (or LLE if you prefer) with this statement made in the Editorial:

Emerging from an analysis of approved drugs, this rubric predicts a compound is more likely to be clinically developable when LipE > 5. [I don’t know what the authors of the Editorial mean by “rubric” (I'm not even sure that they do) but as a reviewer of the manuscript I would have pressed them to justify their claim. Specifically I would have been looking for a literature reference (for me, the choice of the word “emerging” does rather conjure up an image of hot gases and stoned priestesses at Delphi) and a coherent explanation for why a value of 5 yields a better rubric than values of 4 or 6.]

That’s all that I’ll be saying about LipE (or LLE if you prefer) and it’s time to take a look at the contributions of the third nominee for the Nobel Prize in Physiology or Medicine:

Finally, the development of Fsp3 by Frank Lovering in 2009 introduced a new principle for how molecular shape affects pharmaceutical properties and developability. [As a reviewer of the manuscript I would have pressed the authors to explicitly state the new principle that their third nominee for the Nobel Prize for Physiology or Medicine had introduced in 2009. My view is that Fsp3 is a thoroughly unconvincing descriptor of molecular shape and I suggest readers consider the suggestion that cyclohexane (Fsp3 = 1) would have a better shape match with benzene (Fsp3 = 0) than with either methane (Fsp3 = 1) or adamantane (Fsp3 = 1).]

[10-Aug-2025 update: The authors of the CNM2025 study claim "we repeated an analysis similar to that of Lovering et al. to assess Fsp3 in drugs approved post-2009 and those in active clinical development as of mid-2024" and conclude "there appeared to be no clear relationship between highest phase reached and Fsp3, suggesting the key conclusion noted by Lovering et al. has not persisted". My view expressed in this 05-Aug-2025 post is that the analysis is not sufficiently similar to support this conclusion.] 

 

[04-Aug-2024 update: The Fsp3 descriptor had actually been used as i_ali in the YG2003 study (Prediction of Aqueous Solubility of Organic Compounds by Topological Descriptors) six years before the publication of 35:

The aliphatic indicator of a molecule (i_ali) is equal to the number of sp3 carbons divided by the total number of carbon atoms in the molecule.

The YG2003 study discussed prediction of aqueous solubility using i_ali (renamed as Fsp3 in 35) in conjunction with other topological descriptors. In contrast with the claims made in 35 for Fsp3 the YG2003 study made no suggestion that i_ali was a highly effective predictor of aqueous solvation when used by itself.]   

Before discussing the contributions of the third nominee for the Nobel Prize for Physiology or Medicine I should stress that I certainly consider gratuitous use of aromatic rings to be a very bad thing in drug design (it was the data analysis in 35 that was criticized in KM2013 but not the eminently sensible suggestion that drug designers should look beyond what the authors referred to as ‘Flatland’). Having sp3 carbon atoms in a scaffold provides drug designers with a wider range of options for placement of substituents than would be the case for a fully aromatic scaffold and we stated in KM2013 that:   

One limitation of aromatic rings as components of drug molecules is that some regions above and below the plane defined by the atomic nuclear positions are not directly accessible to substituents. Molecular recognition considerations suggest a focus on achieving axial substitution in saturated rings with minimal steric footprint, for example by exploiting the anomeric effect or by substituting N-acylated cyclic amines at C2. 

My view is that deleterious effects of aromatic rings on aqueous solubility would be more plausibly explained by molecular interactions stabilizing the solid state than in terms of molecular shape (this point is discussed in more detail in HBD3). I also see saturated ring systems such as bicyclo[1.1.1]pentane and cubane as potentially more resistant to metabolism than benzene. 

There’s one point that I need to make before discussing 35 from the data analysis perspective which is that molecular structures with basic nitrogen atoms tend to have higher Fsp3 values than molecular structures that lack basic nitrogen atoms (see L2013). This means that you can’t tell whether the benefits of higher Fsp3 values are actually caused by the higher Fsp3 values or by the presence of basic nitrogen atoms.

The Editorial states:

Stemming from an analysis of discovery compounds, investigational drugs, and approved drugs, Fsp3 predicts a discovery compound is more likely to become a drug when Fsp3 > 0.40. [Figure 3 in 35 does not actually depict a significant difference between mean Fsp3 values for for discovery compounds and marketed drugs (the significant difference between mean Fsp3 values is for discovery and Phase 2 compounds).]  

It’s not clear (at least to me) where the figure of 0.40 comes from and I would argue that that compound X (IC₅₀ against therapeutic target = 50 μM; Fsp3 = 0.80) would actually be less likely to become a drug than compound Y (IC₅₀ against therapeutic target = 10 nM; Fsp3 = 0.20). I’m assuming that what the Editorial refers to as “analysis of discovery compounds, investigational drugs, and approved drugs” is what is shown by Figure 3 in 35. Presenting data in this manner hides the variation in Fsp3 for the compounds at each stage of development and makes the trends look much stronger than they actually are (this is verboten according to current J Med Chem author guidelines which state "If average values are reported from computational analysis, their variance must be documented.") I would challenge the suggestion that what is shown in Figure 3 in 35 can be used to calculate the probability that an arbitrary compound will become a drug (my view is that it’s not feasible to even define the probability that a compound will become a drug in a meaningful manner). Analyses of success in clinical development are generally more convincing when comparisons are made between compounds that pass or fail in individual phases of clinical development than between compounds in different phases of clinical development. 

The Editorial continues:        

This observation was ascribed to increased Fsp3 leading to increased aqueous solubility, a critical physiochemical property for successful drug discovery.

I’m assuming that what the Editorial refers to as “increased Fsp3 leading to increased aqueous solubility” is the trend shown by Figure 5 of 35 (this featured prominently in the KM2013 correlation inflation article) which claims to show the relationship between Fsp3 and log S (aqueous solubility expressed as a logarithm).  This claim is not accurate because the log S values have been binned and the relationship is actually between centre point of bin and mean log S value for bin. The authors of 35 used public domain aqueous solubility data for their analysis and we showed (KM2013; see Figure 5) that the Pearson correlation coefficient for the relationship between log S and Fsp3 is only 0.25 (the corresponding value for the binned data is 0.97).  I consider the suggestion that such a weak correlation could have any relevance whatsoever to the the likelihood of success in clinical trials to be wild and uninformed conjecture.      

I'll finish my commentary on Fsp3 by reproducing this claim made in the Editorial:

Much like the Rof5 and LipE, Fsp3 has proven to be enduringly useful for the design of compounds with improved chances of clinical success. (37) [My view is there is insufficient evidence to justify this claim and I'm perplexed by the citation of 37. In any case, members of the Nobel committee are likely to focus more on whether or not Fsp3 is usefully predictive than on the endurance of this molecular descriptor.]  

It’s now time to summarise what has been a long and at times pedantic blog post, and I thank all readers who’ve stayed with me. I don’t consider any of the three studies (22 | 29 | 35) that form the basis of the Nobel Prize nomination to have reported significant scientific discoveries and I would also challenge the claim made in the Editorial that these studies introduced new principles. I’m aware that 22 is heavily cited and I certainly agree that it is common to see values of LipE and Fsp3 quoted in the drug discovery literature. Nevertheless, I would argue that that the Editorial failed to provide even a single convincing example of the Rof5, LipE or Fsp3 making a critical contribution to the discovery of a marketed drug (this should be quite sufficient to rule out the award of a share in the Nobel Prize for Physiology or Medicine to any of these nominees). Furthermore, the Editorial doesn’t provide any convincing evidence that the Rof5, LipE or Fsp3 are usefully predictive in drug discovery projects.

Aside from the failure of the Editorial to demonstrate significant impact for the Rof5, LipE and Fsp3, I do have some scientific concerns about this Nobel Prize nomination. First, the Rof5 is not actually supported by data in the form that it is stated. Second, LipE had already been discussed, although not named, in the drug discovery literature when 29 was published. Third, Fsp3 had been already been introduced (as i_ali) for aqueous solubility prediction and the data analysis in 35 would fail to comply with current J Med Chem author guidelines.