If you attended and took home the message that the future for antibacterial research is to treat persisters, to develop combinations, to target efflux pump gene expression and to use bacteriophage then the meeting probably failed to address the real issues and if this all the UK has to offer we are in a dire situation indeed…… Thankfully this is not the case.
With current global interest in antibacterial resistance and several organisations eg WHO, MRC, BBSRC, EPSRC, NIH, NHS, WT etc in the process of developing their strategies to address resistance and the need for new therapies, I thought it may be helpful to generate a continued online discussion following this timely and interesting meeting and also to let a wider group of colleagues know what was discussed at the meeting.
The first day of the meeting focused on the medical, veterinary and agricultural aspects of antibiotic use and resistance. We heard that interactions between human and animal use of antibiotics fuel antibacterial resistance and that widespread adoption of best practice in animal health could lead to reduced antibacterial usage and perhaps surprisingly improved product yields. A surprisingly large amount of antibiotics are sprayed on crop plants – I had not realised this.
In the UK, aggressive targets to reduce the incidence of MRSA and CDAD were successful although all the reasons why success was achieved were not clear and have not provided any insight to guide future campaigns. MRSA reductions were largely due to a disappearance of one epidemic isolate and no one really knows why it disappeared.
Avoiding use of broad-spectrum antibacterials has reduced the incidence of CDAD but now means that the UK relies on just 4 antibiotics, including carbapenems and piperacillin/tazobactam, to treat the majority of Gram-negative infections. This sounds like a recipe for disaster as their use will inevitably lead to resistance. What do we use then? The answer may be we need to use some of the other antibacterials again and may have to accept a rise in CDAD as a consequence.
Focusing on excellent data for MRSA bacteraemia we learnt that Gram-positive infection is well treated and that the real need is Gram-negatives. While the need for better and a more diverse choice of therapies for Gram-ves is clear, it would have been nice to see some data for other Gram+ve infections (non-bacteremia, non-MRSA) to be certain that the threat of Gram+ves is over. Of note is data on the CDC website that indicates more patients died of G+ve infection than Gram-ve in 2013. Is the USA different to the UK or are we comparing apples and oranges?
Perhaps the community needs to consider we are in this for the long haul and that resistance will be an issue in 300 years and in 1000 years from now. History teaches us that medical need changes, some decades it’s Gram+ves that are causing problems and some Gram-ves. Maybe we need to focus on identifying translatable opportunities based on great science rather than immediate medical need, especially when we consider that it takes decades to take fundamental research to market. We don’t know what the clinical need will be in detail in 30 years.
It would be a shame to over manage the funding environment and to make it impossible to get grants for good Gram+ve work.
Several speakers mentioned the undoubted success of vaccines and thought they should be used more widely. It would have been interesting to have heard from a Vaccine company about the challenges in this area and what they need for the academic community to help.
We also heard that pre-screening patients for carriage of drug-resistance prior to planned surgery and segregation of carriers can prevent spread of resistance. Building better hospital and use of smart materials may contribute over the long term to minimise resistance development and spread.
The second day focused on scientific advances.
Professor David Holden described compelling work on Salmonella persisters – bacterial that reside within cells and are antibiotic-tolerant and once antibiotic therapy stops can grow and cause of recurrent infections (Helaine S, et al., 2014, Internalization of Salmonella by Macrophages Induces Formation of Nonreplicating Persisters, Science, Vol:343:204-208.) While of academic interest, it was not clear that persisters provide a translatable opportunity for novel therapeutic intervention. Recurrent infections are a real but minor problem. I think he mentioned 15% in Salmonella and a different therapy may be needed to reduce persisters in each species. A therapy to reduce persister-driven recurrence may be too niche, difficult and too expensive to progress through clinical trials to reach market.
Should this research be funded? Absolutely. It is cutting edge and internationally competitive fundamental microbiology. But should that funding count towards investment in antibacterial research to address AMR? I don’t think so.
We should also consider the negative effect that focus on persisters has had on TB drug development. For the last decade it has been hard to get funding for novel therapies that target dividing TB in preference for projects that have the potential to sterilise including the persisters. This desireable objective has proven challenging. We now have untreatable extreme drug resistant TB and patients dying with no therapy because we stopped working on pragmatic approaches that treat growing TB that cause the disease. We don't need to repeat this mistake with Gram-ves.
Professor Roy Kishony described experimental studies to better understand the mechanisms of resistance development (Yeh et al. Drug interactions and the evolution of antibiotic resistance. Nat Rev Microbiol. Jun 2009; 7(6): 460–466 and Palmer AC and Kishony R. Understanding, predicting and manipulating the genotypic evolution of antibioticresistance. Nat Rev Genet. Apr 2013; 14(4): 243–248). One theme he developed was how we might choose combinations of antibiotics, for instance seeking synergy and somewhat counter-intuitively hyperantagonism. Doxycycline and ciprofloxacin were used as examples. The latter concept was based on the combination at certain concentrations being slightly less effective than either antibiotic alone. If a bacterium become resistant to one of the antibiotics, at the hyper-antagonistic concentrations, it becomes more sensitive to the second antibiotic and is therefore killed. This approach would select against resistance development. While it all looks good with a single strain on a plate I’m not convinced this concept, or that of synergistic combinations, has any real world application. You have to consider the wide range of MICs in the pathogen population for both antibiotics and to imagine how it would be possible for all strains to dose to the special hyperantagonistic, or even just synergistic, concentrations of the two drugs in combination in patients. Then imagine the metabolic, drug-drug interaction and PK differences in the population of patients on top of strain MIC variability and it just looks unlikely to work in the clinic.
Novel combinations of antibiotics may find uses where they act to reduce by-pass mechanisms and obviously to expand spectrum of activity but trying to be too innovative may not work and pragmatism is likely to be the key.
Professor Julian Parkhill gave an impressive presentation showing that beta lactam antibiotic use selects for target (Penicillin-Binding Protein) changes that contribute to resistance. The quantity of recombination in the real world is remarkable and compensatory mutations are rapidly selected that overcome reductions in fitness.
We heard from GSK to provide a global pharma perspective. Over the last 20-years they have tried everything they can to provide new antibiotics and despite huge investment and talented scientists have not delivered. They have now decided that they need to review alternatives to the small molecule targets single gene target to kill bugs model. This is fair enough and it is good to see that they are willing to introduce rigour and professionalism into otherwise academic and amateur pursuits.
It sounded like they might prefer host eg human targets rather than trying to get drug into bacteria. If suitable human targets can be identified they have a better track record of finding inhibitors. Of course there may be side effects of targeting host functions but it does offer an alternative approach. This may take some time to establish the fundamental biology needed to validate these types of innovative targets and to understand how they might be used clinically. If successful, it would be interesting to know what their timescale for clinical introduction might be? Within 30-years? Within 100?
They will provide industrial quality insight into clinically worthwhile target product profiles and hopefully engage with academics and support the acquisition of key data required to bring alternative medicine approaches such as probiotics, prebiotics, virulence, pathogenicity, bacteriophage and peptides etc from the wilderness into the mainstream if appropriate. There are fundamental questions with each of these approaches that must be addressed before they can be considered suitable alternatives to real antibiotics. There is no guarantee that any of these approaches will find a place in mainstream therapy. Perhaps the best place for them might be in animal and agricultural use to reduce antibiotic usage in these sectors.
With industry appetite at an all-time low, the challenge of taking novel and speculative mechanism of action therapeutics through clinical trials and into use means that only the very best alternative opportunities should be progressed. There is a high degree of scepticism around alternative approaches and any failure will close the door.
We also heard about GSK’s views on how the antibacterial market needs to change in the future. The costs of antibacterial clinical development could be transformed by the appearance of good diagnostics enabling selection of patients for clinical studies. A recent study to demonstrate efficacy in penicillin-resistant Streptococcus pneumonia cost around $1m per eligible patient. This is not sustainable. Being able to recognise the right patients quickly and cheaply could transform development. This is one of the potential outcomes of the recently announced Longitude prize.
GSK also described the need to change the antibiotic prescribing paradigm so that profit is not related to the number of prescriptions. They thought that Governments should fund antibiotic R&D and stockpiling so that they were there when needed. I’m not so sure about this. You never hear of controversy in oncology where doctors oversubscribe cytotoxic chemotherapy after pressure from pharma to write prescriptions. I’m sure this can be dealt with. Furthermore, the recent debacle where the US Government pulled out of a BARDA deal to develop, manufacture and stockpile antiflu therapy means that no organisation will trust Governments in these deals for some time.
We may also need to change our perception of risk and accept that antibiotics may not be as safe as life-style drugs. If safety profiles comparable to cancer cytotoxics were acceptable we might find it easier to bring new therapies to market.
Perhaps improved diagnostics would help here but it can’t be impossible to sort antibiotic prescribing out, even if it is driven by fines if they are use inappropriately. It has to be an easier solution than finding new antibiotics.
GSK’s appearance and open, transparent involvement has to be applauded. Genuinely approachable individuals in David Payne and Lynn Marks, their commitment to precompetitive solutions to the fundamental challenges such as compound entry into Gram-ves, new designs for clinical studies etc have the potential to transform the area.
They briefly described IMI and it was apparent that huge consortia with too many labs, each with too few people is not the way to solve this problem. Investing in visionary leaders and providing them with critical mass of people, resources and time might be.
We heard from Professor Laura Piddock on the challenges of early drug discovery in academia. Her long and distinguished career led her to potentially translatable insights into efflux pumps. Sadly this is an area that has been ploughed before and inhibition of RamA/MarR is a well trodden path eg Paratek. The concept that inhibiting expression of efflux pumps could improve activities of all classes of antibacterials is well established. Finding inhibitors of efflux pump gene expression is possible, but resistance develops very quickly and the concept may have extremely limited utility. When any assay searching for inhibitors of gene expression is performed in highly lab adapted strains of bacterial it is possible to find them. However, even with the use of lab adapted strains containing functional insertion sequences eg. IS1, it is surprising easy to select for strains in which the regulation of a single gene’s expression has been decoupled by insertion of an IS. It no longer responds to normal signals and is now constitutively expressed. It is a small jump to highly recombinogenic clinical isolates – a RamA/MarR inhibitor is unlikely to survive in a clinical environment. The main problem is it just another single gene target and they have proven very hard to crack without resistance development. It will be interesting to learn what this group proposes to do differently to give them a better chance.
The common theme hear is that neither industry or academic have an answer to antibiotic resistance and I would suggest that it is only by working in partnership and by identifying what each can do well and funding them that any significant progress can be made.
Finally we heard from Dame Sally Davies on the UK and Global political scene.
It is clear that Dame Sally has made an outstanding contribution to the global awareness of the need to address this issue with action and I have nothing but admiration for most of what she said. However, she did make points that distract from her otherwise faultless and evidence-based presentation and these merit wider discussion.
Her statement that new antibiotics should be locked away and used with care is a great sound bite but is unrealistic, perhaps unethical and hurts our collective cause. We heard the same limp statements when Linezolid reach the market but it was never reserved. It was used to treat people who needed it. Withholding treatment may make sense at a population level but a physician has to deal with patient in front of them. The statement is also an off-switch to investment from business Angels and venture-capital investors who can share the burden of discovery and development. If they are out then tax payers will have to take on all the risk and pay the whole bill, not just part of it.
Dame Sally also declared that new antibiotics should be available to all globally. Another great sound bite but in reality a recipe for resistance. They should be available for use in all territories who can use them effectively, where secure diagnosis, prescriptions and stewardship are of a sufficiently high standard, where corruption is absent and they can be trusted to work to minimise resistance development and to effectively treat patients rather than make a fast buck. This is not a stick to beat countries with, it is a carrot to encourage them to put their houses in order if they wish to benefit from these valuable resources.
Finally, I think some poor choices were made when she summarised new antibacterial research being funded by the Biomedical Catalyst. Dame Sally has a powerful position and her apparent endorsement for bacteriophage and other alternative therapies sends a dangerous signal to the academic funders that this is the area to invest in.
Highlighting the Biomedical Catalyst investment into Phico Therapeutics as a bacteriophage project misses the point of their unique technology. They go out of their way to try to describe their therapy as a DNA therapy; delivered by a bacteriophage vector. It is probably as far from the Eastern European bacteriophage therapies as you can get.
Instead, she could have chosen to have described the Biomedical Catalysts investment into Cantab Anti-infectives to developed improved Polymixin-based antibiotics to treat Gram-ve infections. This type of project, to improve already effective classes of antibiotic and to rejuvenate them for another 10- or 20-years use has real potential to deliver a clinically useful new therapy within a generation.
As a community over the last 20-years we have learnt that a good target is better than a new target and that a good compound scaffold is better than a new scaffold. We need to use this learning to set our objectives and to inform funding decisions rather than hope that the grass is greener elsewhere and spend another couple of decades idealistically hoping that novelty is the answer.
The UK has great strengths in both the chemistry of antibiotics eg beta-lactams, macrolides, aminoglycosides and polyketides and in the biology of good targets eg penicillin-binding proteins, DNA supercoiling and protein synthesis. Focusing on these as a core for the future of antibacterial research is likely to yield useful and translatable research that could provide new therapies during the next century.