This post will make the case for why eliminating or dramatically reducing prion protein (PrP) is an excellent therapeutic strategy for prion diseases.
Attempts to develop small molecules to treat prion diseases have been aimed at several different targets. A few of the more minor approaches have been aimed at inflammation (indomethacin, dapsone, ibuprofen), excitotoxicity (memantine) and lipid rafts (statins). By far the most popular approach has been to find compounds that (1) prevent PrP aggregation and/or (2) prevent the conversion of healthy PrPC to misfolded PrPSc. In fact, this category includes all of the compounds most heavily investigated in humans (doxycycline, pentosan polysulfate, quinacrine) and several other well-studied compounds (cpd-B, curcumin, amphotericin B to name a few).
By contrast, this post will argue that dramatically reducing the total number of PrP molecules in each cell – regardless of isoform PrPC vs. PrPSc - represents an extremely promising therapeutic strategy.
Reduction or elimination of PrP has already been investigated both in gene therapy and in small molecule discovery approaches. In addition, both active and passive immunization approaches might also deplete PrP, though published efforts at passive immunization have so far been suggested to occlude, not destroy, PrP [White 2003] and it’s not clear to me whether the active immunization efforts [most recently Goni 2008] have resulted in occlusion or destruction. All that is to say, I’m clearly not suggesting anything new here – just gathering in one place the arguments for why PrP depletion is an excellent strategy that deserves even more attention than it is already getting.
In all the prion disease literature, only one study has ever ‘treated’ already-symptomatic animals and managed to reverse the early symptoms of prion disease. I say ‘treated’ in quotes because this was a feat of genetic engineering, not administration of a therapy. Mallucci 2003 created a mouse model of conditional PrP expression. The mice were infected with scrapie at as early as 1 week of age and had already begun to show spongiosis, an early sign of the disease, by their tenth or twelfth week, when their conditionally expressed Cre recombinase gene came to life and floxed the PrP transgene, shutting off PrP expression for good. The mice recovered from spongiosis, never showed behavioral signs of scrapie, and never died of the disease. Later, Mallucci was also able to demonstrate several significant changes in behavior and cognitive capacity had already emerged several weeks after infection and were reversed when PrP was knocked out [Mallucci 2007].
Mallucci’s work was building on an excellent body of literature that came before. Bueler 1993 showed that PrP knockout mice are resistant to prion disease. Brandner 1996 showed that PrPSc isn’t toxic to PrP knockout cells even in an infected brain, suggesting that it is the production, not presence of PrPSc, that is toxic. Tremblay 1998 showed that conditional knockdown of PrP to ~15% of native levels via a tetracycline switch appeared to be enough to prevent any symptoms of prion infection (though a later work by the same group seems to suggest that these mice did eventually succumb to scrapie after 430 days, much later than controls [Safar 2005 (ft)]) [update - on second reading it appears the mice were reduced to ~10% of wild-type PrP expression and did eventually succumb]. In sum, earlier studies had already shown that completely abolishing PrP expression – or perhaps even just knocking it down by a sufficient amount – could prevent prion disease. Mallucci’s work showed that this could also reverse prion disease.
And no other approach has achieved that. The compounds that prevent PrP aggregation or conversion have been shown, at best, to delay symptoms if administered before onset, never to prevent or reverse. In fact, few of those compounds have even been tested in already-symptomatic mice (Pocchiari 1987 (ft)’s trial with amphotericin B is the only small molecule example I am aware of), partly because evidence has suggested that their action is time-dependent, where early administration works and late administration doesn’t work. There’s been a huge disconnect in much of the literature where promising evidence from pre-symptomatic treatment in animals has led to post-symptomatic treatment in humans, with a predictable lack of success. This problem was nowhere more clear than with pentosan polysulfate where Doh-Ura 2004 had shown pretty clearly that the compound had no effect even in late stage asymptomatic animals, yet the compound went on to trials in already-symptomatic humans. The prion research community needs to be serious about the fact that the majority of human prion disease cases are sporadic CJD patients, who will never be available for treatment prior to symptom onset.
PrP is highly conserved among mammals, and conservation often means something is important. We don’t know PrP’s native function [some of the many proposals are reviewed in Aguzzi 2008], and we can’t say exactly what people might be like without it.
But the evidence we have to go on is from animal models: PrP knockout mice [Bueler 1993], knockout cows [Richt 2007], and goats with a naturally occurring nonsense allele [Benestad 2012] are all healthy and viable.
I looked in the literature for any reports of PRNP deletions in humans but only found an example where the deletion spanned another haploinsufficient gene, making it impossible to tell what the phenotype (if any) of a PRNP-only deletion might be. The one report of a PRNP-only deletion in dbVar later turned out not to be real.
So we don’t know what the knockout phenotype might be in humans. But in light of all available animal evidence, it would be quite surprising indeed if knockout were fatal. The knockout mouse phenotypes appear to arise mostly under stress [reviewed in Steele 2007], and while some are quite bad (increased vulnerability to strokes, for instance) it is hard to argue they’re worse than prion disease.
Of course, there could easily be (for instance) subtle intellectual deficits or memory problems, that we wouldn’t notice in mice but would notice in our loved ones. And that risk can certainly be argued as one downside to permanent ways of suppressing PrP, such as lentiviral shRNA-mediated gene therapy, or active immunization, though I’d argue it is still an acceptable risk in the face of the severity of prion diseases
On the other hand, it is worth considering that small molecule and passive immunization approaches would be expected to be both (1) dose-dependent and (2) reversible. These attributes mean that while an extreme knockdown or absolute elimination of PrP might be necessary to reverse a prion infection, a lower dose might suffice for maintenance thereafter, or for preventing onset in genetic prion disease carriers (more on this in point #5 below). Knockdown isn’t the same as knockout: we might expect a subtler phenotype from simply reducing PrP than abolishing it all together.
Compounds that inhibit prion conversion or aggregation have almost always proven strain-specific in their efficacy, to varying degrees. cpd-B was fantastic against RML prions, less effective against Fukuoka-1 prions and did almost nothing against 22L or 263K prions [Kawasaki 2007]. Amphotericin B and MS-8209 worked much better against C506M3 prions than BSE prions [Adjou 1996]. Pentosan polysulfate didn’t work quite as well against Fukuoka-1 or RML prions as it did against 263K prions [Doh-Ura 2004].
Other proposed antiprion compounds may well be strain-specific too – but some of them have never even been tested in more than one strain. For instance, as far as I am aware, all of the animal studies on doxycycline have been done in 263K-infected hamsters [Forloni 2002, Luigi 2008] although some in vitro experiments have been done with other prion strains [Tagliavini 2000].
If these drugs don’t even work consistently across different rodent strains of prions, I question how confidently we can expect them to translate from rodents to humans. And if they do work in some human diseases, I question how likely they are to be universal across FFI, GSS, VPSPr, and the many molecular subtypes of CJD (Type I and Type II strains in MM, MV and VV genotypes). The diversity of human prion strains will continue to pose a problem even if, hypothetically, researchers start doing discovery screens in human cells and animal experiments with mice expressing human PrP in order to optimize their chances of finding human-effective drugs.
What’s more, evidence suggests that even in any one prion disease or in any one patient, what we call “PrPSc” is not in fact one misfolded conformation of PrP but many [Puoti 1999, Polymenidou 2005, Uro-Coste 2008]. Compounds that inhibit the formation of one conformation of PrPSc may still permit the formation of others, resulting in ‘strain selection’ but not an end to disease progression – this has been put forth as an explanation for the therapeutic failure of quinacrine [Ghaemmagami & Ahn 2009]. This suggests that the strain-specific nature of many compounds suggested to prevent prion conversion may not only limit their broad applicability to all prion diseases but may also limit their efficacy in any one prion disease.
In contrast, all evidence suggests that eliminating PrP is a universal treatment. While only one prion strain (RML) has been tested in Cre conditional knockout mice [Mallucci 2003, Mallucci 2007], a central implication of the prion hypothesis is that prion replication requires host expression of PrP. Period. No strain specificity. And indeed, all available evidence supports the conclusion that animals lacking prion protein are resistant to prion disease regardless of strain. The first inoculation experiments on PrP knockout mice showed resistance to RML prions (then called “Chandler prions”) [Bueler 1993] and subsequent experiments have also showed resistance to ME7 [Manson 1994] and Fukuoka-1 prions [Sakaguchi 1995]. To my knowledge, no study has ever found PrP knockout mice to be susceptible to any strain of prion.
As an aside, it’s not yet clear, to me at least, whether or not immunological approaches to treating prion diseases might potentially suffer from strain specificity problems. As far as I can tell, passive immunization efforts in cell culture [Enari 2001, Peretz 2001 (ft)] and mice [White 2003] have all used RML prions, so although the evidence suggests a complete ability to halt PrPSc formation, probably by blocking PrPC binding sites, it’s not clear if the same antibody binding to the same epitope on PrPC would work for all prion strains. Someone who knows more about immunology than I might be able to clarify whether this is a valid potential concern.
In the U.S., the Centers for Disease Control and Prevention (CDC) biosafety regulations for prions require that rodent strains of prion be handled at minimum biosafety level 2; large amounts of BSE or human prions are to be handled “with extreme care in a BSL-2 facility utilizing BSL-3 practices” [BMBL5 Section VIII-h, CDC 2009]. And some institutions prefer to set their own biosafety standards which are yet stricter than those of the CDC.
Biosafety regulations make prion research slower, more expensive and more limited than than it would otherwise be. Our experiences at Prion Alliance have demonstrated that. Our attempts to import FFI knock-in mice from Europe have met with months of biosafety red tape and an elevated cost due to the need for special shipping containers. The first few stem cell institutions that we contacted were unwilling to even handle D178N stem cells. And though we haven’t worked with prions in our lab, I understand it would require an application to a biosafety committee that would need to be extensively reviewed over the course of a few months. All sorts of lab space and mouse space with elevated biosafety levels are at a cost and availability premium, and some things just plain aren’t available – for instance, the drug screening equipment in our lab is BSL1.
To be fair, some of these problems are purely start-up issues and won’t pose an ongoing cost or inconvenience in the long term. Most prion research is done in specialized institutions that have already figured these issues out long ago. But that’s part of the problem: research is limited by the infrastructure already in place. For instance, I suspect that many institutions’ standard requiring BSL3 for research involving human PrP (even in transgenic animals) may be one factor that keeps people doing research on mice expressing mouse PrP (which can be handled more cheaply and easily at BSL2), despite the potential for strain specificity problems discussed above.
Any therapeutic approach for prion diseases will ultimately need to be validated against the real thing – cells and animals infected with prions. But if your goal is to find ways to reduce or eliminate PrP, you can do a huge amount of the initial work at BSL1 in any uninfected mouse or human cell line and then rely on higher biosafety facilities only for validation experiments. That has the potential to save costs and time and make a wider variety of facilities, resources and biological models available.
Above I pointed out that, to the extent that hypothetical PrP-depleting treatments are dosable and reversible, they could work both to reverse disease in symptomatic patients and also to prevent disease in asymptomatic genetic carriers, even if administered at a lower dose than that required for symptomatic patients. This assertion is based on the ample evidence that prion disease incubation times correlate strongly with PrP expression levels: heterozygous PrP knockout mice have extended incubation times compared to controls [Bueler 1993] and mice overexpressing PrP have shortened incubation times [Fischer 1996].
The potential for application both to asymptomatic and symptomatic patients is important first and foremost because we should seek to treat both categories of patient. But even viewed narrowly from the standpoint of wanting to prevent disease in asymptomatic patients, a universal approach is necessary, because drugs that prevent disease will realistically only be approved if they can also reverse disease.
As background, several compounds have shown an ability to delay symptoms or death in animals if administered early enough. If we stringently consider only those small molecule compounds that have shown a delay in onset when administered orally or peripherally in mice infected intracerebrally or carrying genetic mutations, the list is (in chronological order):
- amphotericin B & MS-8209 [Pocchiari 1987 (ft), Pocchiari 1989, Xi 1992, McKenzie 1994, Demaimay 1994, Adjou 1995, Adjou 1996, Demaimay 1997, Adjou 1999, Adjou 2000]
- statins [Mok 2006, Kempster 2007, Haviv 2008 (ft), Vetrugno 2009 (ft)]
- cpd-B [Kawasaki 2007]
- curcumin [Riemer 2008 (ft)]
- memantine [Riemer 2008 (ft)]
- 1,5 diphenylpyrazole [Geissen 2011, Leidel 2011]
- Scutellaria lateriflora [Eiden 2012]
- rapamycin [Cortes 2012]
- astemizole [Karapetyan & Sferrazza 2013]
As someone personally affected by genetic prion disease, I would be thrilled to have a drug that delays onset. That would buy us more time to find a cure. I think that some of these compounds merit further study, though I will argue that if the goal is to find drugs that delay onset in genetic carriers, then the drugs should ideally be tested in genetic mouse models, something which so far has only been done for rapamycin [Cortes 2012].
If, on the other hand, the goal is to find compounds that can reverse the course of full-blown prion disease, the most accurate mouse model is one where already-symptomatic animals are treated, something which, as I pointed out above, has rarely even been tested.
Thus there is a severe disconnect between the way research is done in the lab and the way new therapeutics will need to perform in humans. Experimental new compounds like 1,5 diphenylpyrazole, promising though they may be, have little hope of becoming approved drugs if they cannot reverse disease in symptomatic patients. The rules of human subjects research appropriately allow patients to undergo riskier treatments when they are facing immediate mortality than when they are perfectly healthy.
Consider the story of doxycycline: it delayed disease in animals treated before symptoms [Forloni 2002, Luigi 2008], so it moved on to trials in already-symptomatic patients [see post], where it didn’t show a clear benefit. From there it moved on to a trial in asymptomatic FFI carriers. This sort of ‘workflow’ doesn’t offer us a route to developing new compounds to cure prion disease, for the following three reasons:
- This doesn’t help sporadic CJD patients, who are the majority of prion disease patients.
- Such a trial on healthy asymptomatic carriers is only possible because doxycycline is already an approved drug with tolerable side effects. Such trials do not offer a route to introducing experimental compounds, since healthy carriers’ condition is not dire enough to justify the use of riskier treatments.
- There are so few FFI carriers available for trials like this, and age of onset is so variable, that results will not be available until 2022. While some genetic prion disease carriers will be willing to take doxycycline for the next decade just in case it works, that is, again, only possible for already-approved drugs with tolerable side effects, like doxycycline.
I don’t pretend that I’m saying anything new or controversial here – everyone agrees that what we want is a cure, and that compounds that might delay onset a little bit are just the best we’ve done so far. However, experimental practices do not always reflect this philosophy. Rarely have researchers even bothered to test (or at least, publish) the effects of their compounds in already-symptomatic animals, even though such represent the closest animal analogue of most prion disease patients, who don’t get a diagnosis until they are already in quite bad shape.
Perhaps in some cases people haven’t tested (published) the effects of their compounds in symptomatic animals because they know the answer will be (is) that the compounds don’t do anything helpful for such animals. That needs to change: treatments that are to advance to trials in symptomatic patients should be expected to have undergone testing in symptomatic animals. If you accept that argument, I refer you back to point #1 above: abolishing PrP expression is the only thing that has yet been shown to reverse prion disease in symptomatic animals.
Recently I did a thought experiment: Tremblay 1998 found mice expressing PrP at ~15% of normal levels to be able to produce PrPSc but not experience symptoms of prion disease. So if you had three compounds that could each reduce PrP expression by 50%, and their mechanisms were independent, you could reduce expression to 12.5%, theoretically dropping below some critical threshold where PrPSc production occurs at tolerable levels. Now I’m no longer sure these numbers are correct, because Safar 2005 (ft) implies that Tremblay’s Tet-off mice did eventually show signs of disease, just much later than controls (so late as to occur after the 1998 paper was already published?), so perhaps the critical threshold is yet lower.
Also, of course, it’s unrealistic to expect that different PrP-reducing treatments would behave so multiplicatively. They’ll very likely interact, both in their main effects and in any toxic side effects, so combining drugs is anything but trivial – only experimentation can determine what the combined effect may be.
But the point of this toy example is that once you identify PrP protein expression as the therapeutic target, reversing prion disease becomes a numbers game. It’s possible to combine drugs and measure their collective impact on PrP expression. This provides more of a concrete and measurable ‘roadmap’ towards a cure than combining drugs that interfere with prion replication.
If you agree that reducing or eliminating PrP is a desirable target for treating prion diseases, I believe that does argue for prioritizing some areas of research over others.
First, it argues for prioritizing approaches specifically designed to detect PrP reductions, such as the Lasmézas lab’s recent FRET assay [Karapetyan & Sferrazza 2013]. Screens to discover compounds that inhibit PrP-res formation may be capable of discovering compounds that reduce PrP expression, but they are probably not optimized for doing so. Take for instance the Ghaemmagami lab’s recent screen [Poncet-Montagne 2011]. It identified amcinonide as reducing the level of PrPC via increased degradation, showing that discovering PrP-depleting compounds is possible in such a screen. But if only the top few hits are chosen for follow-up, the attention to such compounds will be diluted by attention to compounds that interfere with PrP-res formation.
Second, it is also unclear, as yet, what length of drug incubation time would be needed to discover compounds that deplete PrP by intervening at a whole range of different points in its lifecycle, from transcription to degradation. Recent screens have incubated cells with candidate molecules for 5 days [Poncet-Montagne 2011], 3 days [Geissen 2011] or 1 day [Karapetyan & Sferrazza 2013]. PrP Tet-off mice took one full week of doxycycline administration to reach their nadir of PrP expression [Tremblay 1998], which I initially took to imply that PrP mRNA has an exceptionally long half-life, though Dr. Corinne Lasmezas has pointed out that this may just be due to pharmacokinetics of doxycycline in vivo. It’s possible that timelines of 1-5 days are already plenty, but more research would be needed to confirm this.
Third, if a reduction in PrP levels is accepted as a prime target, that suggests it ought to be measured in therapeutic experiments. That’s not always the case at present. For instance, the published work on astemizole [Karapetyan & Sferrazza 2013] and on anti-PrP vaccines [Sigurdsson 2002, Goni 2005, Goni 2008] might be well complemented by some quantification of PrP levels in the treated mouse brain. Such a measurement could be an important factor in interpreting why a given treatment did or did not succeed.
Fourth, a goal of PrP reduction argues for more research aimed at characterizing what controls PrP expression levels. In the scheme of the vast amount of research done on PrP, comparatively little effort has gone into figuring out how PrP transcription is regulated, for example. Reports have shown involvement of p53, Sp1 and MTF-1 in a copper-dependent manner [Qin 2009, Bellingham 2009] but the characterization seems far from complete at this stage.
Above all, as I’ve already argued several times, a focus on reducing or eliminating PrP as an approach to reversing symptomatic prion disease argues for a different metric of ‘what works.’ Treatments can be judged in part by how much they reduce PrP, can be combined to achieve greater reductions, and ought to be tested in animal models at the already-symptomatic stage.
Here I have argued that reducing or eliminating PrP represents an extremely strong therapeutic target for treating prion diseases. This is not to dismiss the usefulness of other approaches. Indeed, variety is important and we certainly shouldn’t invest exclusively in one approach. Screens for compounds that prevent the PrPC-to-PrPSc conversion may yet uncover a molecule capable of reversing symptomatic prion disease and working universally across different strains – after all, cell culture experiments with antibodies have suggested that PrPSc production can be halted entirely by binding to the right site on PrPC [Enari 2001, Peretz 2001 (ft)]. Meanwhile, testing drugs to delay onset has already identified a few candidates with well-established safety profiles which may prove useful to carriers of genetic prion diseases.
The points presented here do argue, though, that reducing or eliminating PrP is our strongest potential route towards curing prion diseases. Compared to other approaches, it has more evidence to suggest its potential efficacy and universality; it presents an approach to drug discovery, development and approval that is cheaper, quicker, more rational and implementable. And though we can’t be certain, it seems likely to be safe.
The possibility of reducing or eliminating PrP has already been the basis for experiments in gene therapy and more recently small molecule screening. Further research oriented towards developing treatments to deplete PrP should be a priority in the future.