What is wrong with Alzheimer’s disease clinical research?

There is increasing concern not only in Alzheimer’s disease (AD) research, but all of modern investigations, that false findings may be the majority or even the vast majority of published research claims [1].

Confidence in the findings of a scientific study depend, to a large extent, on establishing a reliable and accurate cause and effect relationship. Cause and effect is loosely defined as two events occurring in succession where the first event is considered the cause of the second event. This encyclopedic definition is often the deadly pitfall of countless scientific studies that contribute to false conclusions. The reason is that hypotheses that rely on cause and effect conclusions often ignore the post hoc ergo propter hoc fallacy, where one event spuriously correlates with another but is falsely deemed to have been caused by the related event. One way of lessening post hoc fallacies is by using causal reasoning. Causal reasoning is the process of questioning causality, for example, by carefully controlling the experimental findings to limit confounding factors or by observing that increased intensity of the presumed cause leads to increased magnitude of the effect.

But what happens when causal reasoning is abandoned in repetitive clinical trials testing the effectiveness of an intervention that consistently yields negative results? This has been the invariable fate of anti-amyloid-β (Aβ) drugs. These drugs were designed to eliminate excessive Aβ deposition in the brain of those afflicted with AD. The drug treatment rationale was based on the Aβ hypothesis, also known as the amyloid cascade hypothesis. This concept has been the prevailing but unproven paradigm in explaining AD causality for the last 20 years. Oddly, there have been more than 100 drugs tested in dozens of clinical trials and not one anti-Aβ drug has succeeded in slowing down AD destructive pathology or prevent declining cognition [2].

The multiple difficulties festering the Aβ hypothesis have been described in countless medical and scientific articles [3]. One lethal blow to the Aβ hypothesis are the numerous clinicopathological studies revealing that heavy brain amyloid deposition does not equate with dementia [3]. Most of the criticisms leveled at the Aβ hypothesis have been largely ignored by big pharma, its supporters, peer reviewers, and granting bodies as if no real challenge could lessen the power of this enduring paradigm. The best that can be said (to paraphrase big pharma executives) is that anti-Aβ therapy display ‘tolerability and safety’ when given to AD patients. But… so does chicken soup. How do any of these help stop the meltdown of AD?

Let’s play devil’s advocate for the sake of balance. What is wrong with pursuing a failed hypothesis? In the case of Aβ, it has provided jobs and resources for researchers who might not otherwise have had the financial capital to keep their labs open; moreover, such monies from big pharma to investigators could even uncover collateral information that could help clarify the process of neurodegeneration. On the other hand, ethical behavior may have been misplaced in this difficult time of financial hardship that threatens research survival.

However, it is unacceptable, in my judgment, when medical researchers (for whatever reasons) steadfastly hold onto a hypothesis that does not help sick patients in any manner despite being paid to do it. Rationalizing such behavior blocks medical progress resulting in dire consequences for the patients’ clinical outlook. Equally disturbing is the callous effect such conduct has on devaluing the scientific spirit and the search for truth.

A forward-looking concern is how to confront the monolithic and insular influence that Aβ research presently holds. Should a failed hypothesis continue to dominate funding research, publications, and conference programs while excluding other research ideas from the think tank? Such thinking requires a game plan whose main goal is not to stop all Aβ research but to open the think tank to other ideas and proposals that might benefit those at risk of dementia. This is a commendable task for graduate students and young investigators to pursue. The brilliant theoretical physicist, Max Planck, argued that scientific progress and evolution of thought does not advance because some inescapable truth is suddenly discovered that replaces the old and useless paradigm. Instead, Planck wrote in his autobiography, “A new scientific truth does not triumph by convincing its opponents and making them see the light, but rather because its opponents eventually die, and a new generation grows up that is familiar with it.”

Let’s not wait for the opponents of new ideas that might replace the Aβ hypothesis to die; there is not much time for the millions facing an AD diagnosis and the agonizing death that follows.

[1] Ioannidis JP (2005) Why most published research findings are false. Plos Med 2, e24.
[2] Sauer A (2014) Has Alzheimer’s research been wrong for 20 years? Alzheimer’s.net, Blog, April 7, 2014.
[3] Kepp KP (2017) Ten challenges of the amyloid hypothesis of Alzheimer’s disease. J Alzheimers Dis 55, 447-457.

Last comment on 15 April 2017 by Markku Kurkinen, PhD


J. L. de la Torre does the field a service by articulating his impatience, which I share, with the continuing focus of so much scientific talent, so much grant and industry funding, on the role of beta-amyloid - to the exclusion of other ideas - in the causation of Alzheimer’s disease. It is easy to agree with his analysis of causation and to value his reference to Max Planck’s impatience with his colleagues of nearly a century ago (though I have never been able to identify the issue that gave rise to Planck's famous aphorism - it wasn’t dementia). And Dr. de la Torre's willingness to be the devil’s advocate for a few paragraphs shows a valuable open-mindedness.

To me the key point (and Jack has made it) is the responsibility we have to millions who are suffering dementia, and to the many millions about to suffer it; and to whoever it is that puts up the funds we spend on our research. The scientific issue will sort itself out, sooner or later; but sooner if we are rigorous and open to new ideas, however uncongenial. And sooner is important to people.

Because there is a non-scientific challenge here, not present in debates on non-medical issues: At what point must we accept a new idea into our thinking? because, however uncongenial to our hopes, it might prove better than our own ideas? and accelerate the treatment or the prevention of a disease? the very treatment and prevention that we promised when we applied for our grants? Sooner is important, morally; to vulnerable people.

I can remember when molecular geneticists located APP on chromosome 21, sequenced it, showed its association with sporadic dementia and with familial, early-onset dementia. And I shared their excitement that they had identified the cause of dementia. But the brain is penetrated by blood vessels at the sub-millimetre level; the cerebral vasculature has to be considered in any cerebral disease. And, when the role of vasculature in age-related dementia is considered, the evidence is (I submit) compelling; Alzheimer’s disease is a small-vessel vascular dementia. A vasocognopathy de la Torre called it, over a decade ago.

Of course any scientist must be free to explore, and to adhere to, any idea, according to our judgement. But freedom always comes with duties; and there is a particular duty on biomedical researchers - to the sick, to the still-healthy, to our benefactors - to stretch our mind beyond the excitement of our own ideas, to embrace those less congenial, with rigour, dispassion, and even passion.

Think about it. Even though the Aβ trials by the pharmaceuticals continue to fall off the cliff, they did have a valid reason to commit millions. Remember, the government and other agencies funded those early academic studies via our trust-worthy peer-review system, while some reviewers covertly blocked the funding and publishing of alternative hypotheses. Let me pose a sensitive question: would a grant/manuscript reviewer approve a contradictory hypothesis and from a competitive institution?

Although I would demand an affirmative response, my personal experience says no. Conflict-of-interest thrives in almost every walk of life, and sadly in our medical/scientific field; perhaps it’s the worse side of Darwinism’s survival. Shouldn’t we expect fairness and objectivity especially in a field that should thrive on novelty; for isn’t that how you define research?

Perhaps I’m wrong, but I believe the oath or duty of a reviewer is to objectively review the work for reproducibility, accuracy, and merit (and budget for grants) while effectively representing other similar supportive and contradictive work in-context. I do not impose my opinion, nor give attention to the author’s names, their institution, and/or funding source.

And so what do we have to show for all those millions/billions of dollars funding the Aβ sink-hole, and for all those peer-reviewers, who protected their own interest by rejecting grants, manuscripts, and other opportunities that propose alternative hypotheses? Apparently nothing to date for the AD patient, and lost time and sour grapes for those with suppressed contrary work.

My feeling is that the peer-review process should either be a blind-blind system (remove names and affiliations) or an open-open system to have a slightly better chance at removing bias, as the current open-blind system allows those threaten to conceal motives, hide behind their reviews, and even obtain fresh ideas. You see, we really don’t have to wait for the grim reaper (as per Jack’s reference to Max Planck), only a new policy to prevent future dead-horse sink-holes.

This comment is from Gary Morris, Ian Clark and Bryce Vissel.

The Amyloid Cascade Hypothesis is simple, elegant and provides a basic framework for hypothetically approaching Alzheimer’s disease (AD), satisfying Occam’s razor. However, often forgotten in the effervescent elegance of the Amyloid Cascade Hypothesis is that many fundamental tenants underlying it have not been conclusively proven. Our deep-seated concerns about this, considering the over-reliance of the field on the Amyloid Cascade Hypothesis, were the catalyst for our recent article [1], in which we do not argue Aβ has no role, but that current data can be interpreted independently of a primary role for amyloid in all AD cases.

We recommend heeding the learnings from other areas of medicine. Billions of dollars were spent on drugs that blocked stomach acid as an approach to cure stomach ulcers. Alternative ideas, such as the idea that bacteria cause ulcers, were widely ridiculed, supported by the weight of evidence of the apparent efficacy of acid blocking drugs. In the end, the Nobel prize winning discovery was that the cause of stomach ulcers was not stomach acid but, in most cases, a different unexpected cause altogether (the cause was bacterial infection of the stomach). So too is it likely to be true that while, like stomach acid, amyloid is likely associated with AD in some way, it is unlikely to be the sole cause, especially as more evidence mounts to suggest that the amyloid hypothesis may not be correct in its entirety. Clearly a broader view of the disease is required.

Importantly, we know little of the normal role of Aβ. We must therefore consider that the role of Aβ and indeed the mechanisms of brain and neurological diseases like AD are unlikely to be as simple as the Amyloid Cascade Hypothesis suggests. Only recently, for instance, have we truly begun to appreciate the breadth of roles non-neuronal cells play in physiological brain function, not to mention the myriad of complex interactions between thousands of proteins, derived from many interacting cell types, including neurons, glia and the extracellular matrix. Many of these interactions converge at synapse, which are highly sensitive to destruction in AD [2].

There have long been outstanding thinkers who have questioned the amyloid hypothesis and despite how it may appear at first glance, the AD literature is packed full of alternative ideas, as we have reviewed [1]. Unfortunately, however, opposing theories have often stagnated, possibly because they have not enjoyed the same levels of attention or devotion (in basic research, by granting bodies, pharmacological companies and even the media) as the Amyloid Cascade Hypothesis. To cite two specific examples of equally plausible Aβ-independent hypotheses of disease, both the presenilin hypothesis and several versions of the inflammatory hypothesis (e.g. [3]) do not need to rely on a model in which Aβ is central [1]. Instead of ignoring these equally valid interpretations of data and in concert with exciting new research on normal brain physiology and pathophysiology, we should aim to embrace these ideas within new theoretical models of AD.

We agree with the comments by Prof. de la Torre that the drivers of this change will be the new generation of AD researchers, who we should aim to bring up on a healthy diet of scepticism of past approaches to enable innovative thinking that integrates current data regarding amyloid with emerging advances in neuroscience, to create a more holistic theoretical understanding of AD. The catch is that this will require dedicated thought, which requires time away from the lab bench, reading extensively. We would like to see more supervisors and PhD committees support that goal.

Bryce Vissel is the Professor of Neuroscience and Director of the Centre Neuroscience and Regenerative Medicine in the Faculty of Science at University of Technology Sydney, Ian Clark is Professor of Biology at Australian National University and Gary Morris is a scientist in Prof. Vissel’s laboratory.

[1] Morris GP, Clark IA, Vissel B (2014) Inconsistencies and controversies surrounding the amyloid hypothesis of Alzheimer's disease. Acta Neuropathol Commun 2, 135.
[2] Morris GP1, Clark IA, Zinn R, Vissel B (2013) Microglia: A new frontier for synaptic plasticity, learning and memory, and neurodegenerative disease research. Neurobiol Learn Mem 105, 40-53.
[3] Clark IA, Vissel B (2015) Amyloid β: one of three danger-associated molecules that are secondary inducers of the proinflammatory cytokines that mediate Alzheimer's disease. Br J Pharmacol 172, 3714-3727.

Dr. Alzheimer's state something to the effect of "The clinics should drive laboratory discovery, not the other way around." Since this other way around is substantially what is done, the results are understandable.  Dr. de la Torre has been trumpeting the AD/CVD connection for decades. Brown University coiled the term "type 3 diabetes" a decade ago. It's clear this is a multifactorial disease. Now the proof comes from the functional medicine side as this mountain of a disease begins to crumble. Guys like Tanzi and Selkoe will or are jumping on the band wagon claiming they knew it all along.  But if they did - which I'm certain they will claim - then they are criminals.

Jack de la Torre's has written an insightful article on the inability, or unwillingness, of researchers in the field of Alzheimer's disease to determine if a target of interest is truly causative of the disease. Specifically as this relates to the beta amyloid hypothesis. Unfortunately, I think this inability to test one's target-hypothesis can be generalized across the CNS neurodegenerative research space, where we presently have only symptomatic therapeutic relief for any of the chronic neurodegenerative indications. What if, in fact, our early conclusion, "that either we find a means to curb further neurodegeneration by means of a neuroprotective agent, or that we must stop the disease prior to disease onset" is omitting another therapeutic strategy that could, for the first time, reverse disease? We have known for over a decade that the adult brain can indeed produce new neurons and seemingly initiate this process in response to neurodegeneration. So the third option would take advantage of the ability by the brain to self-regenerate, however insufficient under chronic neurodegenerative conditions, and push this process in a (i) disease, and (ii) region-specific and (iii) temporal way.

Indeed, this has been Neuronascent's view point all along, in that we take advantage of the highly regulated process of new neuron formation, in select regions of the adult brain, to replace dying and lost neurons in aging and neurodegenerative disorders, i.e. endogeneous regeneration. We are not suggesting returning to the idea of growth factor injections, with the many systemic issues that this often causes. The ideal process-stimulation point should be downstream of growth factors, hormones and other initiators of cellular events. We are also not suggesting administration of general mitogens, that would not qualify as either region-specific or working in a temporal way (i.e. timed to the occurrence of neuronal loss). Instead, the aim should be toward selective therapeutics, that first push neuronal progenitors to not only proliferate (i.e. neurogenesis), but to secondly push the migration and differentiation and thirdly the maturation of neurons -- leading to an associated reversal of behavioral impairment in chronic neurodegenerative disorders. It is time to test a completely new hypothesis, not one based on a single target for neuroprotection in these very complex neuron-dying diseases, like Alzheimer's and Parkinson's disease. The hypothesis to be tested looks at the possibility to pharmacologically push the brain in a safe and non-invasive manner to regenerate itself. This hypothesis could even bring back the possibility of a disease-modifying therapy for Alzheimer's disease patients. It is time to invest in such a paradigm-shift. This is not an issue of a "potential" therapeutic discovery program, years away from human testing. Neuronascent, Inc. already has a patented, neuron regenerative NCE, manufactured for the clinic, that has shown to be safe and which could potentially enter the clinic in 2017.

Judith Kelleher-Andersson, Ph.D., is President and CEO of Neuronascent, Inc. and is the inventor on all of Neuronascent’s technologies.

Comment by Sally Hunter and Carol Brayne

Given the recent failure of the solanezumab clinical trials, it is understandable that discussions relating to the current state of Alzheimer disease (AD) research focus on the failure of the amyloid cascade hypothesis (ACH) and to a lesser extent the presenilin (PS) hypothesis (PSH). For decades the ACH and to a lesser extent the PSH have driven research with the amyloid beta protein (Aβ), proposed as neurotoxic and causal, as the measure of outcome for experimental design. However, there is a third relevant yet almost completely neglected hypothesis, the amyloid precursor protein (APP) matrix approach (AMA) [1-5] that takes a systems biology approach. This hypothesis suggests an opposing view to the ACH, is compatible with a modified PSH, and addresses long standing concerns relating to complexity within the APP proteolytic system.

The AMA starts with the suggestion that APP is a hub [6] and describes how the balance of flow through the various cleavage pathways represents a dynamic and iterative system that receives biological information representing the current state of the cell via regulation of the various cleavages and outputs the integrated biological information via the ratios of its proteolytic fragments. This system can respond to wider changes in the cell by changing the relative proportions of the proteolytic fragments released. Several features support this proposal, APP is constantly expressed, has a short half-life of between 1-4 hours, APP concentration is rate limiting and as a result its multiple cleavages compete. This view predicts that as flow through the β pathway increases, flow through the α pathway (and others) is reduced. Expanding this view, we see that any change in flow through the APP proteolytic system involves both gain and loss in equal measure. Therefore we can never be sure that the physiological changes that we see in experimental systems where Aβ expression is increased are due solely to Aβ – loss of full length APP, loss of the N-terminal sAPPα and P3 from reduced α-cleavage or the loss of sAPPβ’ and Aβ’ from β’ cleavage confounds this interpretation.

In contrast to both the ACH and PSH, which aim to explain the available evidence in relation to the roles of Aβ in AD, the AMA aims to explain the evidence in relation to the behaviour of the entire proteolytic system in both normal and disease states and requires that all the proteolytic fragments are measured. The AMA predicts that the relative ratios of all the fragments are required to describe the state of the APP proteolytic system. This is a major departure from current experimental designs where no study to date has systematically measured these fragments. Exploring this interpretation leads to the conclusion that the confounding effects of all the other proteolytic fragments potentially undermine all current research. An examination of the cross-reactivities of commonly used antibodies illustrates this view [7]. The updated neuropathological diagnostic protocols have suggested that since the monoclonal antibody 4G8 reveals more Aβ pathology it should be the standard antibody used in routine neuropathological diagnosis. However it is not clear where this additional sensitivity comes from or what it represents. This increased reactivity may be due to cross reactivity with P3, the fragment arising from sequential α and γ cleavages, and also cross-reactivity with various catabolic fragments. Further confounding is introduced by the complex molecular behaviours of Aβ and P3 - there is no panel of antibodies that can distinguish between P3 and Aβ across all aggregations states, (monomers, dimers, oligomers and fibrils), across all sequence variations and across solubilities. How then do we best interpret any signal from this or any antibody?

Unlike the ACH or PSH which focus narrowly on evidence relating to β and γ cleavages and interprets evidence from other cellular systems as secondary or as a consequence of these cleavages, the AMA allows evidence from wider cellular systems to drive APP cleavage. Therefore there is no overarching “causal feature” and various factors such as synaptic activity, immune signalling, metabolism cholesterol etc. can be both drivers of and be driven by APP cleavage through complex regulatory feedback. The coherent behaviour of the APP proteolytic system and its regulatory factors can be understood as contributing to a homeostatic point that allows proper cellular function and in the case of neurons, supports appropriate synaptic plasticity. With ageing, the AMA suggests that the APP system becomes increasingly decoherent so that changes in, say, immune signalling or energy metabolism etc. can stress the homeostatic point beyond that which allows full integration of the biological information. Ageing and cellular senescence programs may alter the homeostatic point to which cellular systems cohere [1].  This re-programming of the homeostatic point has relevance to therapeutic approaches that aim to reduce Aβ. According to the AMA, loss of physiologically relevant Aβ may increase flow through β pathways to replace the Aβ removed so that no long term change would be expected and further, flow through the other APP cleavages would be reduced while this adjustment is in progress with further loss of function from other cleavage fragments.

The AMA predicts that each mutation in APP and PS can be understood as altering the homeostatic point or the behaviour of the APP proteolytic system as a whole, allowing changes that happen with e.g. age to impact at an earlier age/stage. Each mutation has the potential to alter the homeostatic balance in this system in subtly different ways. If we take this interpretation further, the AMA predicts that multiple disease pathways are possible, each with different drivers and that those arising from mutations do not necessarily relate to those arising through ageing. Further, the AMA suggests that a detailed investigation of each mutation in relation to neuropathology and cognitive status from a natural history perspective will help clarify how the entire system works – an approach that has not yet been acknowledged as useful.

Because the AMA predicts multiple disease pathways, it also suggests that, unlike familial AD where the presence of a disease associated mutation is a qualitative diagnostic feature, defining sporadic AD as a single disease process in the older population is not possible. Therefore from the perspective of the AMA, there is no way to accurately select sporadic AD cases and controls in randomised controlled trials (RCTs) and any attempt to do so will result in confounding and/or bias.

It is understandable that the wider research community has not fully engaged with the AMA. The AMA was first described in 2005 in a Master’s thesis for the Open University, UK. It was first submitted to a journal in 2006 where it was rejected without peer review. There followed a cycle of re-write, update, resubmit and rejection without peer review until 2012 – journal editors thus denied the AD research community an alternative framework for many years. When work based on the AMA actually gets to peer review, the perspective of the dominant ACH leads invariably to rejection – again blocking access for the wider research community to this alternative perspective. It is possible that other approaches have similarly had major challenges in being visible to the scientific community. There is a reluctance to engage in a constructive way with avenues outside the role of Aβ, including hypotheses relating to the roles of vascular change, the immune system, metabolic regulation, metal homeostasis and oxidative stress etc. in the evolution of dementia.

In terms of strategy in the immediate future, the AMA is clear.

1) In order to fully account for and understand the potentially confounded nature of AD research, we need to accurately describe the APP proteolytic system as a synergistic whole in humans. This will allow us to characterise experimental models in relation to the human so that we can better assess which experimental models of disease are appropriate. Currently this approach is entirely missing from AD research strategy.

2) Experimental techniques to accurately and reliably measure all the proteolytic fragments need to be developed and validated – not a straightforward task given the complexity of the APP system.

3) Since the AMA predicts that rate and timing of APP cleavage is as important as any cleavage products, experimental techniques to accurately and reliably measure protein-protein interactions, affinities and rates of reaction need to be developed, standardised and validated.

4) We need population approaches to generate reliable evidence that describes the APP proteolytic system in ‘normal’ and ‘disease’ states and how this system interacts with wider cellular systems with a view to better defining possible disease pathways in the older population. We may then be able to better select cases/controls for RCTs that reduce confounding and bias.

5) We need to investigate in detail how wider cellular systems interact with the regulation of APP cleavage so that contributions from important hypotheses that have been relatively ignored relating to cellular systems such as energy and metabolism, oxidative stress, immune signalling, calcium regulation etc. can be understood in both familial and sporadic disease.

6) Evidence relating to familial AD arising from mutations requires re-interpretation. Subtle differences arising from each mutation have the potential to increase our understanding of the APP proteolytic system as a whole and crucially, this evidence can be reliably interpreted as relating to an AD pathway since the presence of a fully penetrant mutation is a qualitative diagnostic feature.

Simultaneously following the above recommendations will enable us to better understand the complex problems presented by AD and move towards a rational identification of therapeutic targets. From the perspective of the AMA, we haven’t even started to describe the problem, never mind developing therapeutic solutions.

[1] Hunter S, Arendt T, Brayne C. The Senescence Hypothesis of Disease Progression in Alzheimer Disease: an Integrated Matrix of Disease Pathways for FAD and SAD. Mol Neurobiol 2013.
[2] Hunter S, Brayne C. Relationships between the amyloid precursor protein and its various proteolytic fragments and neuronal systems. Alzheimers Res Ther 2012;4:10.
[3] Hunter S, Friedland RP, Brayne C. Time for a change in the research paradigm for Alzheimer's disease: the value of a chaotic matrix modeling approach. CNS Neurosci Ther 2010;16:254-62.
[4] Hunter S, Martin S, Brayne C. The APP Proteolytic System and Its Interactions with Dynamic Networks in Alzheimer's Disease. Methods Mol Biol 2016;1303:71-99.
[5] Hunter S, Brayne C. Integrating Data for Modeling Biological Complexity. In: Kasabov N, editor. Springer Handbook of Bio-/Neuro-informatics. Berlin Heidelberg: Springer-Verlag, 2014. p. 921-40.
[6] Turner PR, O'Connor K, Tate WP, Abraham WC. Roles of amyloid precursor protein and its fragments in regulating neural activity, plasticity and memory. Prog Neurobiol 2003;70:1-32.
[7] Hunter S, Brayne C. Do anti-amyloid beta protein antibody cross reactivities confound Alzheimer disease research? Journal of negative results in biomedicine 2017;16:1.


When Jack de la Torre asks “What is wrong with Alzheimer's disease clinical research?” I say “Everything”. Writing recently in the Journal of Negative Results in Biomedicine, Sally Hunter and Carol Brayne [1] ask “Do anti-amyloid beta protein antibody cross reactivities confound Alzheimer disease research?” When Watt et al. [2] used SELDI-TOF-MS (surface-enhanced laser desorption-ionization time-of-flight mass-spectroscopy), they found that solanezumab did not bind to Aβ peptides isolated from the brain amyloid, but bound to some 200 other proteins unrelated to Aβ. John Hardy and Bart De Strooper [3] are absolutely right when they write in Brain “The recent failures of the solanezumab … are considerable disappointments … They are causing soul searching in the field: are we on the right track …?”, and some passages later “…with the solanezumab trial and the release of the data, Eli Lilly have done the field an enormous service …” I’ve said it before [4] and I say it again: it should not take more than one experiment to prove a hypothesis wrong. If that does not ring the bell, nothing will.

[1] Hunter S, Brayne C (2017) Do anti-amyloid beta protein antibody cross reactivities confound Alzheimer disease research? J Negat Results Biomed 16, 1. Erratum in J Negat Results Biomed 16, 8.
[2] Watt AD, Crespi GA, Down RA, Ascher DB, Gunn A, Perez KA, McLean CA, Villemagne VL, Parker MW, Barnham KJ, Miles LA (2014) Do current therapeutic anti-Aβ antibodies for Alzheimer's disease engage the target? Acta Neuropathol 127, 803-810.
[3] Hardy J, De Strooper B (2017) Alzheimer's disease: where next for anti-amyloid therapies? Brain 140, 853-855.
[4] Kurkinen M (2017) The amyloid hypothesis is too good to be true. Alzheimers Dement Cogn Neurol 1, 1-9.