Pharmaceutical Innovations: Past, Present and Future

Gordon B. Cutler, Jr., M.D.

Drug discovery has never been easy.  Nearly 2000 years ago, Galen described more than 150 drug products—single and compound products from natural sources, discovered empirically over millenia—that were used by physicians in the Greco-Roman period.  A thousand years ago, the Persian physician Ibn Sina, in his “Canon of Medicine,” recognized that drugs have short-term and long-term effects (both beneficial and adverse), and that dependence of all 4 types of effect on dosage may differ and may also depend on the purity of the original product.


Today, regulatory authorities have approved more than 3000 different drugs, which have produced extraordinary progress against many of the most dreaded diseases.  Advances in all areas of drug development science now provide a continuous stream of new drugs for remaining unmet medical needs. 


Nonetheless, the companies that produced these remarkable new products struggle for survival.  Drug development programs fail at a high rate, requiring each major pharmaceutical company to invest huge sums of money (up to 20% of revenue goes directly into research—in total ~$60 billion annually in the US alone) to support thousands of researchers who pursue hundreds of new drug targets in order to have a reasonable chance of achieving sufficient new drug approvals to pay company expenses and maintain shareowner investment. 


Even so, failure is frequent, pressure to develop “me-too” drugs is intense, innovative products from start-up companies are too few to meet in-licensing demands, and pipeline “dry periods” lead to a steady rate of mergers or acquisitions—even among large pharmaceutical companies.  To paraphrase Hippocrates:  “Patent life short, drug development cycle long, potential opportunities bewildering, selection difficult, mistake perilous.”  The overall cost for each new FDA-approved drug was estimated at $2.6 billion in 2014, and now probably exceeds $3 billion. 


Is there a solution to the current state, or is this the foreseeable future of pharmaceutical innovation?  Hundreds of ideas have been proposed to reduce failure rate, or streamline development, in order to reduce drug development cost.  Many ideas have shown merit, and drug development would be even more expensive without them.  On the other hand, the remaining unmet medical needs are increasingly complex, or affect smaller and smaller populations, and regulatory requirements for both efficacy and safety have continued to increase.  Thus far, the bar has been rising faster than innovation can mitigate, with a relentless increase in drug development costs.


What more can be done?  To answer requires a more detailed examination of development process and the points at which failure occur.  While phase 3 clinical trials receive intense focus because they represent the stage of greatest expense, I would argue that the area of greatest opportunity lies much earlier, at the stage of “target” selection—the stage where management makes an affirmative decision to resource development of a drug against a particular molecular target. 


A drug can be no better than its target, and a fully effective drug against a target of minor importance may nonetheless be inferior to a weaker drug against a major target (for example, calcitonin for osteoporosis, versus any of the bisphosphonates that directly inhibit the bone resorption mechanism). 


What makes an effective target?  Quite simply, an effective target represents a molecular step that is crucial in the biology of the disease process, and that can safely be targeted in humans. 


For some diseases, such as HCV or HIV, the unique viral gene products are so few in number that they could potentially all be targeted and the resulting drugs compared empirically.  Additionally, the underlying biology related to HCV or HIV gene and protein synthesis, or human cell attachment and entry, are more conducive to research and understanding than, for example, the human or vector biology underlying Alzheimer disease, autoimmune diseases, osteoarthritis, malaria, or drug-resistant tuberculosis.  The ability to identify a few targets that are specific to the virus and crucial to their biology accounts for the relatively rapid and extraordinary progress against HIV and HCV infections. 


Similarly, the more complex task (undertaken by the National Cancer Genome Project) of determining and analyzing the specific causative mutations in 12000 human cancers—1000 from each of the 12 most common human malignancies—resulted in the identification of >100 “driving” gene mutations involved in human oncogenesis. 


This trove of new cancer targets is now resulting in new cancer drugs at an unprecedented rate.  Because many if not most cancers are oligogenic at origin, one can envision that personalized drugs targeting a relatively small number of causative mutations in each cancer patient may ultimately lead to profound improvement in survival.  This is a stellar example of profound translational return-on-investment in the basic biology of human cancer pathogenesis. 


How else might we identify effective targets?  A logical approach would be to determine the genes involved in more complex disorders, such as type 1 and 2 diabetes, obesity, atherosclerosis, osteoarthritis, or Alzheimer disease.  But what if the disease appears to results from dozens of common variants that each contribute a slight effect, as appears to be the case in type 2 diabetes?  Which if any of these genes should be targeted, and will it be safe to target them? 


At the current state of knowledge, it seems reasonable to develop drugs against some of the genes that have been identified as having disease-promoting variants.  Variants with small disease-promoting effect may still identify targets for which an effective drug would provide major clinical benefit.  Safety and efficacy will remain at risk, since the drug will likely act in an opposite direction, and with varying effect size, compared to the common variant that led to its identification.


An alternative approach is to discover increasingly rare polymorphisms until all or nearly all of the genetic contribution to each disorder is explained.  Since known common polymorphisms often explain only a portion of genetic contribution, rarer variants with larger biologic effect may exist and provide targets of potentially greater benefit.  The NIH “All of Us Reseach Project,” which will sequence the complete genomes of 1,000,000 US residents—linked to their electronic health records—should provide an opportunity to search for such rare variants with major risk effect. 


Another alternative would be to answer the opposite question:  What are the genetic variants that protect people from disease?  For example, what are the genetic differences between persons with morbid obesity who do or do not have glucose intolerance, insulin resistance, or type 2 diabetes?  Similarly, what are the genetic differences between persons homozygous for apoE4 alleles (who have a >10-fold increased age-related risk of Alzheimer disease) with and without Alzheimer disease by a given age? 


Such resiliency genes have led to new insights into human biology, such as the markedly reduced incidence of myocardial infarction in persons with PCSK9 haploinsufficiency, or the profound increase in bone density and fracture resistance in persons with LRP5-activating mutations.  In the case of PCSK9, PCSK9 antagonists have recently been approved as therapy for familial hypercholesterolemia and patients who cannot take statins, and this new class of drugs has profound LDL-lowering ability even in patients on full doses of statins, and a consequent reduction in major adverse cardiovascular events. 


Each of these two new insights into human biology was achieved through an investment in understanding human genetics, physiology, and epidemiology.  Prior to these human studies, the potential significance of PCSK9 as a drug target for atherosclerosis—or of the LRP5 pathway as a drug target for osteoporosis—had not been appreciated.  These 2 examples are likely just the tip of an iceberg of resiliency genes awaiting discovery.


Identifying resiliency gene variants also mitigates two of the major risks in drug target selection:  first, it provides long-term evidence in humans for target efficacy; second, to the degree that persons with the variants are otherwise healthy, it provides evidence for the target’s long-term safety.  In the case of variants that are relatively common, such as PCSK9 haploinsufficiency (which affects about 6,000,000 persons in the US), the epidemiological evidence for chronic safety can greatly exceed the number of persons, and the duration of exposure, that would ever be possible in a clinical trial.


Selecting targets validated by human genetic and epidemiological evidence for chronic efficacy and safety should improve success rate of drug development and reduce new drug development cost.  However, important risks remain.  A validated target may nonetheless prove to be currently undruggable because of too many closely related targets to achieve specificity (e.g., phosphatases).  Additionally, safety of the target per se does not ensure safety against off-target interactions, which may occur infrequently or after long exposure, and thus appear late in development or after drug approval.  And drugs whose manufacture requires complex biotechnology in sterile plants may still prove too costly in a world with finite resources. 


Let me summarize these comments with a hierarchy of drug development principles:


·         People are more important than projects, in the sense that people should use up projects, and not the reverse.  In a world of finite human and financial capital, a key skill is to know when to move on to the next idea.

·         Projects are more important than techniques/disciplines, in the sense that the project mission should determine the techniques/disciplines employed, and not the reverse.

·         Among disciplines, biology is more important than chemistry, in the sense that biological target validation should drive the search for suitable chemical matter, and not the reverse.

·         Within biology, human biology is more important than mouse biology, in the sense that human target validation should drive the decision to invest in pre-clinical mouse models, and not the reverse.

·         Within human biology, human genetics and human epidemiology to explore human genotype/phenotype relationships—for both disease-promoting and disease-protective (resiliency) gene variants—have proven, and will continue to prove, extraordinarily powerful in validating important new drug development targets.


·         Techniques are more important than results, in the sense that no results at all are better than results obtained with compromised techniques.  There is no substitute for scientific integrity and objectivity.