FIGURE 1: Competing elements that influence target selection
In drug discovery, a research director faces considerable challenges trying to make consistently good decisions concerning target selection. The task is comparable to a treasure hunt with many enticing clues about where to dig, leading often to large, empty holes.
Many perceive the pharmaceutical business as being in a state of crisis. Financial survival and growth mandates the introduction of three or four new chemical entities each year. The gap between that ideal and the reality in achieving such targets gives us and our colleagues nightmares.
Poring through the wealth of genomic and high-throughput data and setting priority targets to maximize profitability sounds like a reasonable approach. But the knowledge base is insufficient to ensure a reasonable chance of success. Exciting targets identified from genomic datasets lack key information, namely, how a particular approach might work in a mammalian system.
DIFFICULT SMART DECISIONS
The right decisions can pay handsomely. AstraZeneca's potent proton-pump inhibitor, esomeprazole (Nexium), is used for treating peptic ulcer and esophageal reflux, resulting in sales in excess of $2 billion within three years of launch. Nexium is the S-isomer of the highly successful racemic omeprazole (Losec, Prilosec).1 Astra scientists were attempting to improve the kinetic yolk of omeprazole by reducing hepatic clearance. Of several hundred compounds tested, only four, including the S- and R- isomers of omeprazole, looked promising. The R-isomer showed the best kinetic profile in the rat. Both the R- and S- isomers of omeprazole were equally potent acid-secretion inhibitors in vitro, and both had equivalent kinetics and potency profiles in dogs. A research director having to decide which isomer to take into human studies might have suspended the program, based on the poor predictive value of the animal data. But a decision was made to compare both isomers in humans and unlike the rat and the dog, the S- isomer of omeprazole had the optimal pharmacokinetic profile.
The PDE-4 isoform inhibitor, sildenafil (Viagra), is another example. This compound was taken forward originally as a novel vasodilator treatment for angina pectoris. In the Phase I clinical trials, clinicians noted that it caused penile erection. Many R&D directors might have rejected the compound as having unacceptable side effects, since there was no defined market for erectile dysfunction at that time. Nevertheless, sildenafil was developed and has been an outstanding marketing success.
Yet another example is the HMG CoA-reductase inhibitor, atorvastatin (Lipitor), which, apart from being more potent than its four predecessors, did not appear to possess significant additional therapeutic advantages as a hypolipidemic therapy. Now its commercial success is the envy of the industry. One can fairly assume that key decision-makers did not anticipate the commercial potential of either line-extension products or the first-in-class sildenafil.
DESIGNED DRUG RESEARCH
What process might improve target selection in order to reduce the current high attrition rate of compounds in development? A selection of the competing elements that influence target selection are listed in Figure 1. Two approaches may help to rationalize this process. First, it is essential to decide what proportion of research resources will be used to discover first-in-class medicines. Here, the proof of concept is established only in well-designed Phase II clinical trials. The balance of resources can be used for "fast following" projects in which therapeutic utility is already established, but the lead compound has one or more shortcomings. Classical examples are the calcium antagonist amlodipine (Norvasc) and the beta-blocker atenolol (Tenormin), both of which reached the market 12th or later in their class but became first in class due to improved efficiency.
Courtesy of Gianni Gromo
Target selection criteria include the plausibility of the hypothesis, feasibility of identifying and testing a selective chemical entity, the risk-to-benefit ratio of the compound, the length of clinical trials, and likelihood that the drug would be an improvement over current therapies. Management must articulate and be transparent about the assumptions underlying their judgments. The Roche Basel Discovery Group now uses multiple-attribute decision analysis (MADA) to develop a prioritization table based on risk-adjusted benefit criteria.2 In regard to the feasibility of the scientific hypothesis, the initial assumption that genomics would have a major positive impact on target selection and validation has yet to be realized. One approach for trying to reduce the signal/noise problem created by genomics is illustrated in Figure 2. The residual gene targets still remain challenging if the organization demands short-term success. Choices have to be made between a few shots at several molecular targets or multiple shots at fewer targets.
Despite its great theoretical promise, rational drug design has not fulfilled its potential. For example, none of the current agents used to treat chronic heart failure – Digoxin, P-blockers, ACE inhibitors, and aldosterone antagonists – were originally designed with congestive heart failure as a target. Furthermore, the design of compounds to increase myocardial contractility by enhancing intracellular cyclic AMP led to increased mortality with the β-1 partial agonist xamoterol and the PDE inhibitors milrinone (Primacor) and amrinone (Inocor).
FIGURE 2: Strategy for reducing the signal/noise problem in genomics.
Of the many challenges facing us concerning target selection, the greatest cause for concern is the hubris induced by the notable advances in molecular biology, which has led to an overzealous reductionist approach to biological systems. As Francis Crick has remarked, "In contrast to the basic laws of physics, the laws of biology are often only broad generalizations, since they describe rather elaborate chemical mechanisms that natural selection has evolved over billions of years."3
We must balance our approaches by focusing on understanding complex systems. Significantly improved medicines often arise from speculative projects, which can be validated only by Phase II clinical trials. Therefore, resources should be set aside for translational medicine, including the study of specific compounds which of themselves may have shortcomings, making them unsuitable for commercialization, but which can be used to establish proof of concept in the relevant disease. Smith Kline & French administered the first H2 antagonist, burimamide, to volunteers, demonstrating that it inhibited histamine-stimulated acid secretion even though the compound was only active by intravenous administration. Similarly, the ACE inhibitor teprotide, which could be given only intravenously to patients with severe hypertension, resulted in blood-pressure reduction.
The strengths and weaknesses of the molecular or the 'integrated' biological systems approach to drug discovery has been elegantly described by Mark Lindsay.4 The molecular approach relies either on the genetic or molecular analysis of clinical samples or cultured cell systems, in which genetic expression or gene modulation become the basis for target identification. The alternative biological systems approach relies on either studying the pathophysiology of disease in patients or the creation of animal models using forward or reverse genetics. Lindsay concludes, "The most significant problem in relation to target discovery is the multifactorial nature of the chronic diseases that are presently the focus of many companies." Thus, the identification of disease-relevant phenotypes at the biological system level would seem to offer the optimum starting point for target identification.
Perhaps the most difficult challenge relates to the need for an attitudinal change for those who invest in the pharmaceutical industry, which is perhaps the most controlled, highest-risk industrial enterprise. In the current operating climate, both investors and financial analysts are growing impatient with the perceived problem of deficient R&D pipelines.
One consequence of the current investor attitude, which expects short-term double-digit growth from the industry, is a degree of precipitancy in target selection in order to provide "good news" for the investors. Research and development organizations within the pharmaceutical industry must be accountable for performing efficiently and effectively. Yet for the reasons discussed, the discovery and development of significantly improved medicines cannot be achieved within a "command economy culture."
That is not to say that much needs to be done in large pharmaceutical companies to improve efficiency, but this is not the same as improving effectiveness. At one stage in the field of space exploration, NASA adopted a strategy of "cheaper, faster, leaner," the result of which was the loss of an $800 million Explorer spacecraft due to failure to retest the software controlling the landing phase. Perhaps for the pharmaceutical industry there are limits to the cheaper, faster, leaner command-economy approach. But successful target selection is an inherently difficult and lengthy process, because nature will never give up its secrets easily, either in health or disease.56
Desmond Fitzgerald is an independent consultant in drug research from Cheshire, UK. He can be contacted at
Gianni Gromo is the head of Discovery Research, and deputy site head at F. Hoffmann-La Roche in Basel, Switzerland. He can be contacted at