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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’, 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 11 February 2017 by Thomas Lewis, Ph.D.


Submitted by Jonathan Stone, DSc on

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.

Submitted by Michael D'Andrea, PhD on

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.

Submitted by Bryce Vissel, PhD on

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.

Submitted by Thomas Lewis, Ph.D. on

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.