Barts-MS rose-tinted-odometer: ★
I sit on several steering committees and advisory boards for projects that are exploring remyelination or recovery of function as a treatment strategy in MS. Doing this allows you to think or groupthink, which has prompted me to consider whether remyelination in MS is necessary or not. I have been scratching my head about why in 2020 three remyelination strategies failed.
- High-dose biotin (MedDay) – Effect of MD1003 in Progressive Multiple Sclerosis (SPI2) (ClinicalTrials.gov Identifier: NCT02936037)
Primary outcome: Proportion of patients Improved on either the EDSS or 25TW
- Bexarotene (Cambridge University) – A trial to determine bexarotene’s safety and tolerability and its ability to promote brain repair in patients with multiple sclerosis (EudraCT number 2014-003145-99)
Secondary or remyelination outcome: Change in mean lesional MTR between month 0 and month 6 for lesions selected for each patient.
- Opincinumab (Biogen) – Efficacy and Safety of BIIB033 (Opicinumab) as an Add-on Therapy to Disease-Modifying Therapies (DMTs) in Relapsing Multiple Sclerosis (MS) (AFFINITY) (ClinicalTrials.gov Identifier: NCT03222973)
Primary outcome: Overall Response Score, a multicomponent score based on 4 components: EDSS, T25FW, 9HPT in the dominant hand and non-dominant hand.
Have we the MS community made a fundamental mistake in assuming that remyelination is an ongoing persistent problem that needs fixing in MS? Have we got the biology wrong? Is biotin-dependent mitochondrial dysfunction and biotin-dependent remyelination pathways a problem in MS? Is the activation of retinoid X receptors (RXRs) to promote remyelination the correct target in MS? Is the inhibition of an inhibitor of remyelination with opicinumab (anti-LINGO-1) sufficient to promote remyelination across the central nervous system? At least with anti-LINGO-1 or opicinumab, there was proof of biology, i.e. the drug did improve conduction speed in demyelinated optic nerves.
Were the trial designs correct? For high-dose biotin, the population of pwMS was quite old with a lot of disability. Maybe the population was too old and hence ageing mechanism prevented any recovery of function from being detected. Maybe there was too much axonal or nerve loss and hence remyelination was doomed to fail.
Maybe focusing on the individual MS lesion with bexarotene using MRI techniques is too fickle? It is clear that in the bexarotene study there were too few new, presumably actively demyelinating, lesions to generate a signal.
The overall response score in the opicinumab trial may not be good enough to capture the recovery of function due to remyelination. The idea of using a composite score to detect recovery of function makes clinical and biological sense. However, using the limbs as the main read-out may not be sensitive enough. What about vision, cognition, balance, bowels, bladder, fatigue, etc. Do we need a better outcome measure? Do we have to go back to the drawing board with our clinical outcome measures?
Or is the answer staring us in the face? When you treat MS early with the big guns, i.e. alemtuzumab or HSCT, it is quite remarkable how many pwMS have spontaneous recovery of function. Are alemtuzumab and HSCT doing something fundamental to the pathogenesis of MS that then allows for spontaneous recovery of function? Are we curing a proportion of people with MS with these treatments?
One of the latest theories that is being tested in MS is that because of premature ageing and senescence the oligodendrocyte precursors and oligodendrocytes (myelin-producing cells) can’t function properly. The solution is to reprogramme them, i.e. dial back the ageing clock by using diet (caloric restriction, intermittent fasting or ketosis) and/or medication (e.g. metformin or fumarates) before hitting them with drugs to stimulate myelin formation. The latter is backed by animal data, but will it work in MS? Possibly; however, this is based on the assumption that the tools we have for measuring remyelination in pwMS actually work.
The danger with all these strategies is tossing the baby out with the bathwater, i.e. once a trial is negative with a compound it is very rare that the community goes back to the compound or biology. So we need to be confident that our methods are sound and reliable. I am not sure we can be that confident after the three failures above.
Another aspect that is lacking in all our trials is neurorehabilitation, i.e creating the biological stimulus to promote recovery of function. Nobody would perform a spinal cord injury recovery of function trial without active rehabilitation on top of the treatment being tested. The latter is backed up by sound science and compelling animal studies. Why do we in the MS community expect spontaneous recovery of function without rehab? If you don’t use it you lose it! To encourage the recovery of function you need to stress the pathway. I thought this concept would be a no-brainer, but I have yet to convince one Pharma company to add-on a rehab programme to their recovery of function trials.
Maybe instead of trying to promote remyelination and recovery of function in pwMS, our aim should be to treat MS effectively early on, i.e. to prevent the need for remyelination therapies in the first place? The question is how do we get the wider MS community to promote the use of alemtuzumab and HSCT, or similar agents, as the default first-line therapy for MS? Some of us have tried, including me, but have failed miserably with this seemingly easy task. By the time most pwMS get to alemtuzumab or HSCT, they have so much damage that they need restoration therapies.
As we think we now know the potential cause of MS trying to put out a fire without correcting the upstream pathology is folly. Therefore maybe we should only be trying remyelination and neurorestorative therapies in people who have stable fixed deficits, with no ongoing evidence of any inflammatory disease activity, post alemtuzumab or HSCT? The irony of letting pwMS become disabled before being treated with alemtuzumab or HSCT is inadvertently creating a trial-ready population of subjects for remyelination therapy trials.
I encourage thoughts or counter arguments on the above. Let’s have an open discussion and debate on the points I have raised in this post. I think we need to answer some fundamental questions about remyelination and neurorestorative therapies before we spend more money on futile trials and throw the baby out with the bathwater.