The Carnegie Lecture, University of Glasgow, Scotland. March 6 2019
On Translational Science — The Alchemy of Turning Science into Medicine
By Gerald Chan
You can tell from my bio that I am a man with a checkered past. A kinder self-evaluation I have devised is to count it my good fortune to have been able to pack several careers into one lifetime.
Among my disparate careers, I was once a practicing scientist. I find myself back being a scientist now, albeit, no longer working at the bench. In my first scientific career, I aspired to publishing in journals like Nature and Science, and I did. In my current scientific career, my work is measured neither by the quantity nor quality of publications. The goal of my work is to get novel drugs approved and into the clinic. The reviewers that judge my work now are not the peer reviewers judging for journal publication acceptance. They are the reviewers of the FDA, or Food and Drug Administration, the American federal government agency that regulates medicines. They hold the submissions before them to a much more stringent standards for materials, processes and data reproducibility than what is generally practiced in academia. Rather than novelty of the science, the FDA reviewers judge only on the safety and efficacy of the candidate drug under review. (Throughout this lecture, I will refer to the FDA as the regulatory body not only because I work primarily in the US, but also as representative of all government regulatory agencies such as the European Medicines Agency here in Europe.)
When I worked at the bench, my research was on a very narrow topic. Today, the science that I do covers a broad sweep of the life science landscape – biochemistry, immunology, oncology, microbiology, virology, pharmacology, toxicology, neuroscience, analytical chemistry, medicinal chemistry, structural biology, antibody engineering, biologics manufacturing, biostatistics, data science and artificial intelligence. This breadth by no means implies that I am an expert in all of these fields. What is required of me to do my job well is to see the various aspects of a project through the lens of each of these disciplines and to construct an integrated picture of the whole. The work is not only reductionist, the way most modern science is done, but also integrative. From my first to my second scientific career, I traded depth for breadth. Being one afflicted with attention deficit, this is a tradeoff that I find quite agreeable.
When I worked in the laboratory, my work was with a model system of cultured cells. Today, the experiments I am involved in are done on humans, otherwise known as clinical trials. In vitro assays are the beginning, animal data provide supportive validation, but only human data count.
Instead of writing grant proposals to be peer reviewed, I now worry about finding co-investors to support my projects whether they be fellow venture capitalists or managers of family offices, mutual funds, crossover funds or sovereign funds. Some of them are scientists with incisive insights into various aspects of drug development, others are pseudo scientists, former scientists, failed scientists, or outright non-scientists whose sole objective is to use science to make a financial gain.
Finally, in my first scientific career, the projects were open-ended. There were no pre-determined outcomes, as there never should be in pure scientific inquiries. They were unconstrained explorations led only by data. In contrast, my current work is entirely teleological – there is one and only one objective and that is to fulfill what the FDA prescribes for getting a drug approved. While this single telos for all the projects may seem constricting and monotonous, any peril of boredom is more than offset by a portfolio approach to my work. The number and variety of companies that I work with and the possibility of starting new companies with new science provide for an endless supply of intellectual stimulation punctuated, as reality would always have it, by setbacks and disappointments. I will come back at the end of the talk to give some flavor to the variety of projects I am working on.
What I propose to do in this lecture is to offer a glimpse into the workings of biotechnology as an endeavor in translational science. When I was a student, the term translational science had not yet been coined. It is a fairly recent term used to describe the work of taking scientific discoveries and further developing them into useful products, policy, practice or social impact. As far as benefit to society is concerned, advancement in science remains inconsequential to the public until science is translated. For the purpose of the talk today, I will limit myself to the translation of life science into medicine. I use the term medicine broadly to include all that which restores health to the sick or enhances the physical and mental wellbeing of people. Within biotechnology, this includes diagnostics, drugs or therapeutics, vaccines, gene therapy, cell therapy, medical devices and more.
Notwithstanding the recent origin of the term translational science, the spirit of translating science to become tangible benefits to society was present in the early days of modern science as evidenced in the founding documents of the Royal Society. Partly because the tools of science were still primitive in the seventeenth century, utility was in fact one route to knowledge of how nature works. Vaccination is a prime example. Long before there was any understanding of immunology, Edward Jenner did his cowpox vaccination work. What Jenner did was in essence bypassing all preclinical work that would be required by the FDA today and went straight into a human clinical trial. The same was true with Louis Pasteur’s work on rabies vaccine a century later. Today, to put utility into practice without prior understanding of the underlying science is rare. Modern science has evolved to be predominantly about mechanistic elucidation from which utility is devised. Therefore, within the scientific establishment, there is a treasure trove of scientific discoveries that hold promise of benefiting society if only more resources can be devoted to translational work. It was this promise that spawned the biotechnology industry.
I think it would be neither possible nor productive for me to give you an overview of the biotechnology industry. That would be a survey a mile wide and an inch deep. Instead, I propose to use the case study method this evening to tell the story of biotechnology. I will describe my investments in a couple of biotech companies in recent years. Even in doing this, I will not be able to offer much detail for lack of time, but will instead focus on the thinking behind some of the critical developments in those cases. Through this exercise, there are several points that I would like to highlight.
The first is the convergence between science and medicine. While science has plenty of white space that has no overlap with medicine, at least not yet, the future of medicine is critically dependent on science. Furthermore, beneath seemingly unrelated clinical specialties, there is science that is common to them. A prime example is immunology threading through infectious disease, cancer, autoimmune and inflammatory diseases.
Second, whether a translational project of turning science into medicine is successful is not decided by the scientific community collectively, but by the FDA alone. In turn, the FDA has laid down a well-defined path of how to get to a successful translational outcome. It has its own set of internal logic which forms the basis for a regulatory regime. A scientist may be highly acclaimed for a scientific discovery, but it does not mean that he or she is the right person to lead the effort to translate that discovery. Prosecuting the translation of science into medicine calls for specific skills in how to navigate this regulatory path.
Third, standing between novel laboratory findings and novel clinical medicine is a series of high-stakes investment decisions and scientific judgement calls. It is high-stakes because this translational process is long – usually requiring a decade or more, very expensive – usually requiring hundreds of millions to billions of dollars, and has a binary outcome. This long process consists of a series of sequential steps with no short-cuts and limited leeway for parallel processing. The determinants of success or failure, some foreseeable and others not, are innumerable and interlocking. It is no wonder that in spite of the best planning by the best minds, clinical trial outcomes are fraught with surprises. Financial capital that comes with a tolerance for such unquantifiable risks is always in short supply.
What is critical, therefore, is the decision of what projects to bring forward. Once the commitment is made to go down this long journey of translation, there is limited room for making changes without severe financial penalty. My colleagues and I review up to five hundred proposals each year from which we make two or three new investments. Those who are new to the business are easily dazzled by each proposal brought before them, usually in a highly polished presentation made by clever and passionate founders. To be discerning calls for the decision makers to have seen the entire pathway of how science becomes medicine many times before so that they have some foresight of the challenges that the current project will likely encounter. They have to make a determination whether the challenges are surmountable, and if so, the cost thereof measured both in terms of financial cost and time. Time is important because of the finite life of the patents that protect scientific discoveries. The task is to envision the future with the clarity of hindsight. There is no formulaic guide to making such decisions. There is only an alchemy of scientific plausibility, technical feasibility, financial affordability and the likelihood of generating a return in the future for the capital put at risk.
Let me begin with the first case of an oncolytic virus. As the name implies, this is a virus that kills cancer cells. Ten years ago, I came across a company named Biovex which was developing a genetically modified Herpes Simplex 1 virus such that the virus can only replicate in tumor cells. The company was out raising an extension of its series G financing, meaning that it was the eighth time the company was out raising money. In other words, the company had burned through a lot of cash. It had started out as a neurology company. When its programs were unsuccessful, the company changed course to develop an oncolytic virus. Because of these earlier failures, series G could only be raised at a highly dilutive valuation, meaning that the investments of the earlier investors were basically wiped out. Thy could either accept the severely punitive financing terms which valued their earlier investments at somewhere around fifteen cents on the dollar or the company would go under.
At that time, the company had made a modified Herpes virus and injected it intratumorally into fifty patients with metastatic melanoma in a Phase 2 clinical trial. These patients were covered with skin cancers all over their bodies. Two things stood out from those results. There were no serious side effects to the treatment other than flu-like symptoms. A quarter of the patients had objective response noted as either Complete Response or Partial Response by the clinically accepted RECIST criteria. These designations are defined as either complete disappearance of the target lesions or that they showed at least a 30% reduction in lesion size. Interestingly, the majority of the lesions that disappeared or were reduced in size were lesions not injected with the virus.
Against these seemingly encouraging results were mitigating circumstances. The FDA had never approved an oncolytic virus before. There was no guarantee that it ever would. Viruses had always been thought of as something bad for human health. To inject a virus for therapeutic purpose seemed rather radical. As to the company Biovex, it was teetering on the verge of running out of money. If it succeeded in raising this round of financing, it could go into Phase 3 clinical trial. If not, all the tantalizing Phase 2 data would not be able to save the company from collapse. To get to the next value inflection point, the company needed close to a hundred million dollars. Would I commit this kind of money to a management that had done nothing for their earlier investors, a management that seemed to always spend more money than what is agreeable with the frugality inculcated into me by my Chinese forebears?
To make a long story short, I did invest. Why? I based my decision on two accounts – safety and efficacy, exactly what the FDA cares about. On the score of safety, beyond the obvious fact that there were no serious adverse events among the fifty patients in the Biovex data, I thought that oncolytic virotherapy represents a paradigm shift from the safety profiles known hitherto in chemotherapy and radiation therapy for cancer. To put this into perspective, one needs to go back to the history of cancer chemotherapy which had its beginning with nitrogen mustards and other cytotoxic chemicals — poisons, in essence. Many of them were DNA damaging agents or agents that interfered with the cellular machinery needed for a particular phase of the cell cycle. They therefore kill preferentially cells that are cycling, in other words, proliferating cells and that is what make up tumors. The same is true for ionizing radiation. Because there are organ systems in normal physiology that also depend on the continuous proliferation of certain cell types to maintain normal function, there is a price of collateral damage to be paid for killing the cancer cells. This is why patients undergoing chemotherapy lose hair, have their gut lining disrupted and therefore have diarrhea, are anemic and at risk of infection because their red and white blood cells are not replenished. Chemotherapy is therefore always subject to a therapeutic window – too little drug and the cancer is not eradicated, too much drug and the therapy kills the patient. This therapeutic window has been the nemesis of chemotherapy.
With the advent of recombinant DNA techniques, it became possible to genetically manipulate a lytic virus such that viral replication depends on metabolic functions that are active in tumor cells but not in normal cells. This is why the virus will only kill cancer cells and not normal cells. For the Herpes Simplex 1 virus, this meant deleting the gene that blocks the interferon response in the host cells. Since the interferon response is typically defective or lost in cancer cells, the Herpes virus can only replicate in cancer cells. For an adenovirus, tumor cell selectivity comes from the deletion of the early viral E1A gene which activates the Rb/E2F pathway that is needed for viral replication. In cancer cells, this same pathway is constitutively active, hence the virus can only replicate in cancer cells. For a vaccinia virus, the tumor selectivity comes from the deletion of the viral thymidine kinase gene which is needed for viral reproduction. The host thymidine kinase gene is expressed only during S phase in normal cells but is constitutively expressed in high levels in cancer cells from the activated EGFR-Ras pathway.
I thought this kind of genetic manipulation of the virus to selectively kill the cancer cells was orthogonal to all former attempts to overcome the therapeutic window such as targeted delivery of the cytotoxic drug, varying the dosing regimen or selectively protecting the normal tissues. It was an elegant solution that had the potential of changing the therapeutic window into true tumor selectivity. Of course, by 2009, targeted therapies using small molecule kinase inhibitors were already in the clinic, but I had thought that cancer cells could always mutate around such targeted therapies and therefore the response would not be durable. I thought the same for therapies based on cancer specific cell surface receptors such as Her2/neu targeted by the antibody drug Herceptin. Under selective pressure, the cancer cells can lose the receptor and use alternative growth stimuli. After all, the progression of a cancer may be considered as accelerated evolution through hyper-mutability to escape growth control. In retrospect, my judgement was probably a bit too harsh as the survival benefits of targeted therapy drugs are clinically meaningful. But it was this line of thinking that kept me from investing in kinase inhibitors and made me all the more excited about oncolytic viruses.
On efficacy, the fact that Biovex saw regression of uninjected tumors immediately suggested to me that these results were immunologically mediated. Bear in mind that this was 2009; neither the immune checkpoint inhibitors of CTLA4 and PD1 nor car-T therapy had been approved yet. Attempts to remove the brakes of the immune system such as inhibiting SOCS1 and Cbl-b had not yielded convincing results, neither had attempts at adoptive transfer of lymphocytes or the administration of interleukins. Perhaps the most promising results that kept the hopes for immunotherapy alive were still the ones published by William Coley around the turn of nineteenth to twentieth century. He injected cancer patients with live or heat-killed bacteria to induce an infection and saw their tumors melt away. In spite of such case reports of successful immunotherapy appearing in publication sporadically, immunotherapy had never become a mainstay of clinical oncology. To me, the Biovex data looked like immunotherapy had finally turned the corner.
Our working model was that tumor lysis by an oncolytic virus results in tumor antigens being picked up by antigen presenting cells so that the host can mount an immune response targeting the tumor cells. This model overlooks the intricacies of the interaction between the viral and the host genomes. We didn’t know about the Herpes virus activating the STING pathway. It may be that activating STING is more important in why Herpes oncolytic virotherapy works. We also had thought that by engineering the gene for GM-CSF into the oncolytic virus, it would help to recruit dendritic cells to the tumor microenvironment. This also turned out to be questionable. These as yet unresolved mechanistic intricacies highlight an important point — the FDA does not care about mechanism of action. It is a nice-to-have, not a must-have. All that matter to the FDA are the functional endpoints of safety and efficacy. A recent example is FDA approving ketamine as a fast-acting anti-depressant when it’s mechanism of action in the brain is still unknown. I have seen projects where the originating scientists had become overly focused on the mechanistic novelty or elegance of their work. As far as the FDA is concerned, that is barking up the wrong tree. Herein is a fundamental difference in the outlooks of a basic scientist and that of a translational scientist.
Fifteen months after I invested in Biovex, on the strength of the Phase 2 and the as yet unfinished Phase 3 trial, Amgen came along and offered a billion dollars to acquire Biovex. Amgen then put in the financial resources to complete the Phase 3 clinical trial and T-Vec became the first oncolytic virus to be approved by the FDA.
The nice financial outcome aside, I had always thought that there would one day be multiple oncolytic viruses in the clinic just like there are multiple chemotherapeutic agents. At that time, there were numerous companies developing oncolytic viruses on the backbones of adenovirus, vaccinia virus, reovirus, pox virus, myxoma virus, coxsackie virus, vesicular stomatitis virus, and even an attenuated poliovirus. This is good because from work done on vaccines, it is thought that heterologous prime-boost using different vectors to deliver the same antigen works better than using the same vector for both prime and boost.
For my second act in oncolytic virotherapy, I surveyed the oncolytic virus space and found a small, struggling company named DNATrix that was founded by researchers at MD Anderson Hospital in Houston, Texas. This company was developing a modified adenovirus as an oncolytic for glioblastoma multiforme, or GBM, the cancer that felled Senators Ted Kennedy and John McCain, and here in Britain, my friend the Labour MP Tessa Jowell. The GBM indication particularly interested me because the Achilles heel of oncolytic viruses is that it cannot be administered systemically. The host immune system clears any viruses found in circulation, especially a virus against which the host has antibodies from prior exposure. GBM is always focal and therefore most amenable to local administration of the oncolytic virus.
From the standpoint of clinical trial design, the probability of relapse after surgical resection of the primary tumor in GBM patients is almost certain. The time to relapse is also very predictable. Once relapsed, time to death is short under available standard of care. While it sounds callous to say this, these are exactly the characteristics that make for good clinical trial feasibility. Betting against near certainty makes it easier to show an efficacy signal than betting against a highly variable outcome. A faster readout means savings in time and cost. The Phase 2 clinical trial of DNATrix is ongoing.
I would like to turn now to the second case, a portfolio company that is working in the innate immunity space. To put this case in perspective, I’d like to say a brief word about the history of immunology. From its early days to its heyday, almost all immunology research was focused on the adaptive branch of the immune system. The other branch of the immune system, what is called innate immunity, was thought of as the primitive “evolutionary leftovers” and the “dumb” part of the immune system. Consider the second half of the twentieth century when immunology went from crude serology to discovering the clonal selection of immunity, antigen presentation, major histocompatibility complex, antibody structure, rearrangement of immunoglobulin genes, affinity maturation, class switching, recognition of self / non-self and transplantation rejection, and so on. These discoveries had resulted in Nobel Prize after Nobel Prize. It was a period of explosive growth rarely seen in any branch of science in any period of time. In the face of such a barrage of earth-shattering discoveries elucidating the adaptive branch of the immune system, there was little interest in innate immunity.
In a landmark lecture given at the Cold Spring Harbor Laboratory in 1989, the immunologist Charles Janeway posited that our understanding of adaptive immunity had reached an asymptote and that it was an experimental artifact from the use of Freund’s adjuvant that masked the role of innate immunity in initiating the adaptive immune response. He called the adjuvant, a messy preparation of killed bacteria containing a gimish of bacterial products like lipopolysaccharide, the immunologist’s dirty little secret. He further proposed that the innate immune system works by a pattern recognition that is used both for recognizing pathogens and self / non-self. He invoked Thomas Kuhn to characterize his pronouncements in that lecture as a scientific revolution. Immunology took a turn and the mysteries of the innate immune system began to come to light.
A major component of the innate immune system consists of a set of circulating proteins collectively known as complement. They are known as complement C1, C2, C3 and so forth. They recognize and tag pathogens for destruction through a cascade of activation of members of the complement family. A company named Alexion took an antibody that inhibits complement C5 into clinical trial in 1997, initially for rheumatoid arthritis and autoimmune disorders. Neither gave an efficacy signal. A physician in Leeds thought this antibody would work for a rare disease named paroxysmal nocturnal hemaglobinuria, or PNH, the prevalence of which is 16 cases per million people. He tried the antibody against complement C5 in eleven PNH patients and it worked like a charm. Fast forward, that antibody was approved by the FDA in 2007 for treating PNH. In commercial launch, the drug was priced at US$400,000 per patient per year and these patients require lifelong use of the drug. It became the most expensive drug in the history of pharmaceuticals.
I cite the Alexion case not because I endorse the practice of pharmaceutical companies setting stratospheric drug prices, a practice that I rather detest, but to show that medicine follows science. If immunology had not made the turn from only studying the adaptive immune system to studying the innate immune system, all the complement-based therapies would not be possible. Beyond PNH, Genome-Wide Association Studies have shown a linkage between complement C3 and age-related macular degeneration (AMD). Complement C4 has been shown to be associated with schizophrenia. C4 may in fact have a role in pruning neurons during development. Who would have thought that these “primitive” proteins floating around in circulation play such important roles in functions like vision and cognition which are associated with higher organisms? The connection between the laboratory and the clinic does not always fit neatly into the prevailing scientific paradigm.
In 2011, I met a brilliant young physician scientist who saw that as much as the Alexion antibody stopped hemaglobinuria in PNH patients, it was still leaving many patients anemic and in need of periodic blood transfusion. He thought that inhibition of complement C3 which is upstream from C5 would be a better strategy. On that hypothesis, he founded a company named Potentia with small investments from angel investors. He also worked on C3 inhibition as a therapy for retarding macular degeneration of the eye. This work attracted the interest of the ophthalmology company Alcon which licensed the C3 inhibitor from Potentia and put it into human eyes in a safety clinical trial. Unexpectedly, the peptide fell out of solution and crystals were floating in the vitreous of the injected eyes. Alcon returned the intellectual property to Potentia, leaving it a company with a failed molecule and no money.
The easy thing to do for any investor is to ignore such walking dead. I would argue that there is a lot of valuable information buried in the land of the dead if one does the forensics. Second attempts can be less risky than the first because those who went before had marked off some of the death zones. However, glamor is never on offer in the land of the dead. The drug development business is not above fads. At any given time, there are some hot disease areas or drug targets that herds of companies will go after. Companies that are not in with the crowd command lower valuations and have a harder time attracting investors. The same may be said when a company works on a project that is vastly ahead of its time.
Unlike my first investment in Biovex, when I led the first institutional round to invest in Apellis, the successor company to Potentia, there were no human safety or efficacy data to rely on. The science was all there was to go by. It would be two more rounds of financing totaling over a hundred million dollars before a clinical signal was obtained. Today, Apellis is engaged in three Phase 3 clinical trials and the company, listed on Nasdaq, is valued at a billion dollars.
In drug development as in science, it is easy to plead conservatism, couched as prudence, and recoil from taking risk. This is the mindset of the majority of people. I cannot overemphasize the need for independent thinkers who can form their own conviction from empirical evidence. Such evidence that underpins risk-taking rarely comes neatly packaged. Evidence tend to be scattered about and needs to be curated, corroborated, interpreted and extrapolated. The robustness of such evidence requires both depth and breadth. Drilling deeply into a narrow topic, however intellectually seductive it may seem, may in fact obfuscate alternative pathways to the same clinical outcome and mislead in risk assessment. Connecting the dots across a broad scientific landscape including a longitudinal view of the progression of science over time is necessary for constructing a robust context for charting a course into the unknown.
I have often wondered whether this capacity to choose an unpopular course of action in science comes from nature or nurture. I have no definitive answer, but am inclined to think that at least in translating science into medicine, an appropriately designed course of study can go a distance to producing professionals that are fit for purpose. I used to think that a MD/PhD program would be suitable but am no longer of that mind. I would therefore like to propose a new degree at the doctoral level that is a practice degree rather than a research degree, meaning that the degree is intended to prepare people to go into practice rather than to go into research. The thinking behind this proposed curriculum comes from my years of being in the practice of translating science into medicine and learning on-the-job. Perhaps a formal training course will facilitate more bright minds to go into translational science.
Currently, further training in science is by the PhD degree which is a research degree. Of necessity because of time and funding constraints, the scope of a PhD thesis project has to be well-circumscribed. Training in science beyond a first degree is indeed necessary for translational scientists, but spending three years on a narrow research topic is not optimal.
Separately, the MBA degree for business is probably the most highly developed practice degree. I used to recruit fresh MBA graduates from several top business schools in America. It was by sampling products of different styles of MBA training that I became convinced that the best way to prepare people for business is by the case study method pioneered by Harvard Business School. More than ever, now that any information can be had from the internet, what separates the men from the boys, so to speak, is how information is processed and what one can do with it. I submit that the case study method is the best way to so train the intellect.
With the case study method as the pedagogy, I propose a new doctoral program in translational science consisting of three domain-based modules — biomedical science, regulatory science and business.
For the biomedical science part, the training would be by reading research papers and critiquing them. In other words, rather than using cases specifically written for case study in business schools, one practices case-based learning using published scientific papers. Both the choice of papers and the content of the discussion should be in the context of science being brought forward in translation. Much like the case study method in business schools, people who teach by the case method must be specifically trained to do so.
The regulatory science module has to do with the FDA’s prescribed pathway to get a new medicine approved. This includes the Chemistry, Manufacturing and Controls, or CMC, requirements as applied to small molecules and biologics, quality requirements such as Good Laboratory Practice (GLP), Good Manufacturing Practice (GMP) and Good Clinical Practice (GCP), biostatistics and clinical trial design, and medical writing for regulatory submission. Once again, I advocate the case study method to explicate why previous submissions to the regulatory agencies succeeded or failed.
For the business module, the cases would cover intellectual property law, structure of licensing and partnering deals, market launch of pharmaceutical products, pharmaco-economics, product distribution and pricing , and ethical issues in the pharmaceutical industry. Both the strategy and finance of start-up biotech companies and big pharmaceutical companies should be examined.
The course would consist of two years of concurrent coverage of these three domain areas, all by the case study method. The third year would be field learning carried out as internship in companies, government agencies, NGOs, patient advocacy groups or grant-making charities. This experience would culminate in a thesis based on the internship work. Here, I am influenced by the restructuring of the Doctor of Public Health, or DrPH degree at the Harvard T.H. Chan School of Public Health, a practice degree as distinct from the PhD, a research degree which the School also grants.
I know that starting a new degree program this ambitious is a daunting task. Setting ambitious goals is agreeable with me, involuntary regression to status quo is not. I put this idea out there in hopes that some university will pick it up and implement all or parts of it. It would be a big service to science and medicine.
I had said in the beginning of this lecture that my work offers an endless stream of stimulation because of the possibility of starting new companies with new science. I like to conclude by giving you a sampling of some interesting companies that I have started in recent years and that we are still working on.
Hepatitis B — about 1% of chronic carriers of HBV spontaneous clear the virus each year as measured by the disappearance of the S antigen. Why? We think we have figured that out and can induce that clearance.
Vaccine for bacterial pneumonia — there is a fifteen-valent vaccine on the market which is a polysaccharide vaccine and it costs US$200 per course of vaccination. This is not affordable by developing countries. I have tried for nearly ten years to make a cheaper vaccine.
Autism diagnostic — using data mining techniques on behavioral measurements, we can diagnose children who are on the autism spectrum with near-100% sensitivity and specificity compared to the current clinical gold standard. Earlier diagnosis means earlier and more effective intervention. Two of this company’s projects have been granted Breakthrough status by the FDA.
Gut microbiome — we isolated a strain of commensal bacteria from the feces of a healthy individual that makes a metabolite capable of killing only clostridium difficile, a bad commensal bacterium in the gut that causes severe inflammation. This is a novel alternative to developing new antibiotics which has not been successful for too many years.
3-D printing of pills to achieve bespoke pharmacokinetics for combination of drugs — this is applicable in two cases where we are combining two approved drugs to achieve a clinical outcome. In one case, two old drugs are combined to retard disease progression in ALS patients. In another case, two old drugs are combined to eliminate sleep apnea. Needless to say, the repurposing of old drugs has large impact on reducing healthcare cost.
Mitochondria medicine — by improving mitochondria function as measured by the generation of ATP, this small molecule drug, still in Phase 3 clinical trials, has improved mobility and vision for patients carrying mutations in genes involved in mitochondria function.
So, there you have it, a few tidbits from my work in translating science into medicine. It would be wonderful if more people can be inspired to make this their career as I have found mine to be intellectually stimulating and rewarding. The call from the bedside is for more science and more translation of science into medicine. Therein lies the hope for finding solutions to as yet unmet medical needs.