What is Aβ?

The search to find therapeutic targets in Alzheimer's disease (AD) has been dominated for over 25 years by research into the roles in the initiation and progression of dementia of the amyloid beta protein (Aβ) [1, 2], derived from the β-pathway of amyloid beta protein (AβPP) cleavage. This has been driven by several lines of evidence:

  1. the genetic evidence from familial forms of AD (FAD) where fully penetrant mutations in the presenilin (PSENs) and the amyloid β precursor protein (AβPP) genes are qualitative markers of disease and are associated with younger ages of disease on-set [3];
  2. the neuropathological deposition of Aβ in senile plaques and as cerebral amyloid angiopathy associated with dementia in both FAD and sporadic AD [4, 5];
  3. evidence from animal and cell culture models of AD based on the genetic mutations.

Taken together, the evidence has been interpreted to give Aβ a causal role in the development of dementia in humans and that modulation of Aβ is a primary therapeutic target. This approach has never been fully accepted by the AD research community [6-12] and epidemiological population based studies of ageing consistently find complex relationships between age, amyloid pathology, in-life factors such as education, and dementia status [13-17]. The recent failures of clinical trials demand that we re-examine the amyloid approach in detail. Of particular relevance to this re-examination is the question - What is Aβ?

Superficially, this question seems irrelevant - the body of literature reporting on Aβ in AD is vast and Aβ is assumed to be a well-defined molecular concept. However, when mapping the AβPP proteolytic system from a systems biology approach it becomes difficult to assign a single node to "Aβ" [18] suggesting a more complex model is required.

The first difficulty is the heterogeneity of what we understand as the Aβ amino acid sequence. Most researchers accept that Aβ40 and Aβ42 have different associations with AD; however, a detailed investigation of Aβ-related AβPP proteolytic fragments in experimental settings reveals a multitude of associated soluble peptides [19] few of which have been systematically investigated with respect to AD. Some fragments are known to cross-react with commonly used antibodies introducing confounding in interpretations of immunoassays and immunohistochemistry for Aβ, of which the perhaps most concerning is the confounding by P3-40 and P3-42 (derived from the alternate α-pathway of AβPP cleavage) in cerebrospinal fluid based biomarkers relating to C-terminal Aβ and in neuropathological diagnostic protocols using the anti-Aβ antibody 4G8 [20]. Despite known reaction with various antibodies raised against the Aβ C-terminal, no study has investigated the extent of confounding due to P3-42 and/or P3-40 with these antibodies. The enhanced reactivity profile of 4G8 when compared to both 6E10 and 6F3D illustrated in Alafuzoff et al [21] may be due to its reactivity with P3 type fragments in addition to Aβ- type fragments. The current practice of interpreting immunoreactivities seen with commonly used antibodies as "Aβ" without controlling for the other fragments misleads the entire amyloid based research approach. What do these different reactivities mean and how do we translate findings relating to Aβ between studies using different antibodies? Are we all measuring the same Aβ?

A second difficulty is the heterogeneity of Aβ aggregation state, including monomers, dimers, oligomers and fibrils. No experimental approach currently measures Aβ in all possible aggregation states so that any measure of Aβ may be missing specific aggregations with particular relevance to oligomeric forms. Aβ-type fragments of any sequence length in any aggregation state in relation to AD have not been systematically investigated in humans.

Considerations of P3-42 highlight a third difficulty - that of solubility. Evidence suggests that while P3-40 is seen in the soluble compartment, P3-42 is not [19], though it has been detected neuropathologically in fleecy amyloid deposits [22]. Differences in solubility are also seen between Aβ40 and Aβ42. The consequences of these differences in solubility and the effects of compartmentation remain to be clarified.

A fourth difficulty arises due to post translation modifications of Aβ. Taking the immunoreactivity profiles of the anti-Aβ antibodies 6E10 and 6F3D seen in human brain tissues [21], beyond considerations of aggregation state, is the lower reactivity of 6E10 also associated with N-terminal truncations or other modifications [23]? What significance do these modifications have for the physiological roles of Aβ?

A fifth difficulty arises when assigning functions to specific fragments from the AβPP proteolytic system. Most investigations focus on Aβ alone without taking the complexity of the AβPP proteolytic system into account however, this neglects the contributions from full length AβPP and other proteolytic fragments derived from AβPP including the N-terminal sAPPα released following α-cleavage and sAPPβ released following β-cleavage. Given that AβPP is rate limiting [24], any change towards the β-pathway that results in increased production of Aβ-type fragments necessarily involves loss of function in full length AβPP and/or α-pathway. It then becomes difficult to assign causal roles to gain of function of Aβ without controlling for loss of function in full length AβPP and/or products of the α-pathway. Our understanding of the roles of Aβ in AD is currently confounded by our lack of understanding of how Aβ sits within the wider context of the whole AβPP proteolytic system [18, 20, 25].

The research community as yet has no systematic approach to the definition of Aβ either in theory, e.g., how many nodes are required in a systems biology based model of the AβPP proteolytic system—or in practice—e.g., which Aβ are we measuring in immunoassays? Aβ is currently a poorly defined concept associated with multiple confounding factors which undermine our understanding of "Aβ". Without an understanding of what Aβ is, we cannot say what roles Aβ plays in human AD with any certainty with important consequences for amyloid based research. Despite strong pressures to include amyloid based immunoassay biomarkers in clinical settings, none are specific enough at a molecular level to take account of sequence, aggregation state, solubility and post translation modifications, none have been validated in the human population, and their diagnostic and prognostic usefulness is uncertain [26]. It is essential to identify and clarify ambiguities in our understanding of the amyloid based approach if we are to understand the recent failures and build a better foundation for future research. It is now well past the time for the AD research community as a whole to have an open and honest discussion, however difficult that might be, to re-visit the decades of accumulated evidence. What do we actually know about the roles of "Aβ" in all its isoforms in AD and how do we know it?

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Last comment on 1 May 2018 by Sally Hunter,


Sally Hunter deserves our gratitude for her blog post detailing the uncertainty we have about the molecular and immunological characteristics of the Aβ proteins at the center of the dominant so-called amyloid cascade hypothesis of Alzheimer’s disease. What is most refreshing is her attempt to see the molecular phenomena embedded within a systems biology perspective, as well as pointing to broader (and indispensable) contexts such as public health and epidemiology. She deserves further plaudits for her persistence in getting her message across and effectively aligning her concerns with a growing body of other wisely skeptical voices. She focuses on the need for more complex models at a molecular level. If more space were available she could have expanded on how little we know about the normal function of the Aβ related proteins in healthy brain function.

The amyloid cascade hypothesis is not merely a scientific hypothesis, it is more often used as a political statement. It is illuminating to compare this alleged hypothesis to the so-called cholinergic hypothesis that was dominant for a period before Alzheimer’s became more the subject of molecular biological and genetic focus. Is the cholinergic hypothesis true? We are told hypotheses need to be tested by trying to reject the null: can it be rejected and, if so, using what criteria? Clearly, there are loss of cholinergic neurons and nicotinic receptors in several types of dementia. The preclinical and clinical evidence that cholinergic systems are involved in memory and attention is strong. And cholinomimetic drugs were approved by the FDA on the basis of well-designed studies, although we can argue in retrospect that their effectiveness in clinical practice is minimal.

It appears that the amyloid hypothesis suffers from similar problems. How could we reject the hypothesis? In the clinical diagnostics and drug trials space with which we are familiar there have been repeated failures over the past decade. Now the claim is often made that we just need to apply our therapies earlier (now in people with so-called elevated risk as demonstrated on an amyloid PET scan) and study their effects for longer durations and with higher doses. Money has been wasted on poorly designed evaluations of the imaging methodology itself. Hundreds of millions of dollars were allocated by the Centers for Medicare and Medicaid Services to try to determine whether the experts who advocated for the investment could evaluate in an unblinded nonrandomized situation whether they found the test useful. Not to mention that the scans are often difficult to interpret—even in the hands of “experts”. Individuals who received the scans were only told that their risks were either elevated or not. Reasonably, they might ask “how elevated”? One might expect quite different reactions from people whose scans are said to be either positive (elevated) or negative, by neglecting that the imaging measures of amyloid actually exist on a continuum rather than being a binary. People receiving these scans tend to believe it is a “test” for Alzheimer’s (it is not—it is a test for amyloid) and hence have unrealistic sense of the importance of the scan.

Our fear is that the political pressure to get an outcome from the amyloid hypothesis, i.e., prove it is true and the enormous financial and time investment worthwhile, is so great that it is, as others like the late Mark Smith have suggested, “too big to fail”. If we are not careful, we will let the FDA yield to pressure to approve drugs on the basis of un-validated biomarkers. The tearful and angry marketing message that creates fear that our healthcare system will be overwhelmed by Alzheimer’s disease and related disorders may be used to try to justify doing something even if it is close to nothing (and an expensive nothing at that!). For example, the Alzheimer’s Association advocates the development of medications to end or cure Alzheimer’s and extrapolates hundreds of billions of dollars of cost saving, while at the same time using modeling with the drug priced at zero [1,2].

Fortunately, we are now finding that there are many interventions that can improve quality of life for people with dementia including behavioral, educational and arts-based approaches. Do we really only have to only “care today” expecting to “cure tomorrow”? Or should we recognize that regardless of what we do medically, improving our care for each other is more important than pursuing illusory goals of cure.

And now we are talking about drugs to prevent Alzheimer’s disease and there is much hype in this field of prevention that we need to critically evaluate. Yet, there is enough evidence to support so-called lifestyle and community interventions that developing policies to enhance such programs appears reasonable, even in the absence of large-scale randomized controlled studies. Dietary modifications, physical exercise, meaningful cognitive activities, and social engagement all likely contribute to improved brain health and resistance to age-related cognitive loss. These are not specific for heterogeneous groups of conditions like Alzheimer’s disease or even dementia more generally but rather are good for a variety of age-related conditions including those involving the heart.

The problem with these kinds of interventions is mainly that they do not glitter in the way that efforts to cure diseases bedazzle us. These often promised but rarely delivered biomedical approaches produce a glitter which is ultimately fool’s gold and the real “gold” goes to those in the Alzheimer’s field who make irresponsible promises while ignoring genuine opportunities to address the individual and social challenge of dementia at a local, state, and national level. The amyloid hypothesis is ultimately about politics; it’s about false hope and it’s about irresponsible behaviors and profit motivated corruption of values that should be central to our research efforts. We need to understand more deeply the consequences of economic and political forces to commodify and financialize the brain and the rest of our lives (i.e., neoliberalism). Appreciating the social determinants of health and enhancing our collective commitment to one another are essential to addressing the real challenges of Alzheimer’s. In those processes we also have the opportunity to learn important lessons about what it means to grow old and in fact to be a human being within an interdependent community in increasingly vulnerable ecosystems.

Peter J. Whitehouse and Danny George

[1] Alzheimer’s Association (2015) Changing the Trajectory of Alzheimer’s Disease: How a treatment by 2025 saves lives and dollars. http://www.alz.org/documentscustom/trajectory.pdf
[2] Whitehouse PJ, George DR (2016) A Tale of Two Reports: What Recent Publications from the Alzheimer's Association and Institute of Medicine say about the State of the Field. J Alzheimers Dis 49, 21-25.

I thank Peter Whitehouse and Danny George sincerely for their very generous comment. The wider issues they raise are important and reflect the diversity of perspectives in Alzheimer’s disease (AD) research. Each of the questions they ask could fill many pages with discussion. However, my intention here is to examine a very narrow part of one narrow approach to AD research. Even though the amyloid beta protein (Aβ) has been a focus of intense research for over two decades, the concept of what Aβ is lacks clarity both in theory and in laboratory practice – hence the title of the blog.

As Whitehouse and George suggest, if space had allowed I would indeed have included considerations relating to the physiology of Aβ and further expanded this to include the wider APP proteolytic system – I could have asked the question “What is Aβ and what is it doing?” However, understanding of the physiology of Aβ depends to some extent on what we understand Aβ to be. As others have asked before, is it a neurotoxic culprit, neuroprotective [1] or is it a perfectly normal part of our complex human physiology? As an example, Aβ has been associated previously with long term depression (LTD) as oligomers [2] and as larger aggregates [3] in synaptic plasticity and this physiological feature has been interpreted as a measure for Aβ neurotoxicity [4]. However, if we view Aβ in the wider context of the APP proteolytic system as a coherent whole, there is a case that the actions of Aβ balance with the physiological actions of sAPPα – that of promoting long term potentiation (LTP)[5]. We can then see the APP system as part of the dynamic regulation of synaptic plasticity with Aβ playing an appropriate role. The evidence we currently have for the involvement of Aβ in LTP and LTD can be interpreted to support both views, so how do we tell between them? I suggest that we do not have the evidence with the depth of detail required to answer this question with certainty. Given the current state of AD research and its move towards defining AD in terms of biomedical models, there seems little interest in investigating exactly what we mean by the term Aβ as though this question has already been answered, when in fact it hasn’t.

The reduction of the complexity of (AD) to a few biomedical “markers” of disease, one of which is Aβ, raises many issues relating to the diagnosis of AD at the individual level that are challenging and as yet unresolved. Whitehouse and George quite rightly highlight the difficulties in assigning binary diagnostic cut off points to what are continua of pathological changes. Although AD-related pathologies, including tau-associated neuritic plaques and tangles and Aβ-associated plaques and deposition as cerebral amyloid angiopathy are considered as “diagnostic” in the sense that the presence of these neuropathologies confirm a clinical probabilistic diagnosis of AD, the relationships between dementia status and neuropathology seen in the older population - where most dementia occurs - are complex. The associations between dementia and pathology do not fully support the interpretation of any AD- related pathology as being qualitatively diagnostic - having a positive score for an amyloid- (or tau-) associated biomarker does not correspond to having AD-type dementia with certainty nor has prognostic value of these measures been proven [6]. Diagnostic protocols highlight ambiguities in how AD is defined and understood by different research approaches. AD can be defined in many ways, as a clinical entity, as a neuropathological entity, as a genetic entity for familial forms, as a combined clinicopathological entity and as a clinicopathological entity with biomarkers. However, no single definition is currently agreed by all researchers and not all definitions translate well between research approaches. Issues relating to AD definitions have been previously explored by Whitehouse (https://www.j-alz.com/editors-blog/posts/is-there-alzheimers-disease ).

I hope those with diverse perspectives outside the immediate biomedical models of AD based on Aβ will forgive this narrow consideration, it has to be narrow in order to re-think what we mean by Aβ and how we understand its roles within wider contexts. Our understanding of what Aβ is and what it is doing depends on flexibly integrating contributions from many research perspectives. I suggest that we in the AD research community have a collective responsibility to examine the evidence relating to Aβ accumulated so far in detail including considerations of limitations arising from straightforward issues such as anti-Aβ antibody cross reactivities and the more complex issues surrounding how the definition of AD impacts experimental design in different experimental approaches.


1.            Bishop, G.M. and S.R. Robinson, The amyloid paradox: amyloid-beta-metal complexes can be neurotoxic and neuroprotective. Brain Pathol, 2004. 14(4): p. 448-52.

2.            Wang, H.W., et al., Soluble oligomers of beta amyloid (1-42) inhibit long-term potentiation but not long-term depression in rat dentate gyrus. Brain Res, 2002. 924(2): p. 133-40.

3.            Chiang, H.C., et al., Distinctive roles of different beta-amyloid 42 aggregates in modulation of synaptic functions. FASEB J, 2009. 23(6): p. 1969-77.

4.            Koffie, R.M., B.T. Hyman, and T.L. Spires-Jones, Alzheimer's disease: synapses gone cold. Mol Neurodegener, 2011. 6(1): p. 63.

5.            Ishida, A., et al., Secreted form of beta-amyloid precursor protein shifts the frequency dependency for induction of LTD, and enhances LTP in hippocampal slices. Neuroreport, 1997. 8(9-10): p. 2133-7.

6.            McKhann, G.M., et al., The diagnosis of dementia due to Alzheimer's disease: recommendations from the National Institute on Aging-Alzheimer's Association workgroups on diagnostic guidelines for Alzheimer's disease. Alzheimers Dement, 2011. 7(3): p. 263-9.



I happened to see this interesting posting and thought I could also briefly comment, since I have been working on this complex "Abeta" fpr quite some time. I fully agree that we do not know as much about Abeta as it often appears when one reads about anti-Abeta therapies, the amyloid cascade hypothesis, amyloid  brain imaging, etc. I also fully concur that nomenclature is very important and that misunderstanding about Abeta antibody-specificities has been a problem. However, it is not easy to implement more accurate terminology broadly, since APP processing and the various N- and C-terminal types of Abeta, p3, etc, are quite complex and, for example, not something an amyloid brain imaging researcher might spend much time with. The drive to simplify is strong. It is particularly important to understand the differnce between amyloid (aggegated thioflavin positive plaques) and Abeta (a normally generated peptide). However, these terms are still frequently used interchangeably. Another comment is on the topic of p3 and  the numerous other APP/Abeta fragments. There have been quite many studies characterizing different Abeta species over the past decades and going through this large literature is not easy. What happens mostly is that cherry-picking takes place at some level. Scientific studies are  never complete and perfect, in particular in retrospect. As someone who has spent many years studying these complex aggregation-prone peptides, observations that have been made but are not widely appreciated include that p3 is remakably difficult to find particularly in brain, and that neurons prefer the beta-cleavage pathway, compared to most other cell types, which cleave mainly at the alpha site (e.g. papers from the Beyreuther lab in Heidelberg from the 1990s and also one of my earlier ones, Gouras et al., 1997). Here I could mention that reference 19 in the initial post, from Rong Wang and colleagues (1996), was from non-neuronal cells. In addition, , the excellent Thal et al. paper (1999; reference 22) could not definetly define  the N-terminus of the Abetax-42 they detected. I can also mention that when we have used the term "Abeta42", we do not mean to imply that this represents Abeta1-42; it just is shorter than to always write Abeta x-42 (this includes p3 and I understand that then "Abetax-42" is not ideal). Nomenclature  could certainly be more precise. More emphasis might have been given in this discussion to the more recent advances in biomarkers/imaging, which are teaching us quite a lot, such as that specifically Abeta42 drops in CSF as the earliest biomarker in AD. Also the findings that the presence of amyloid in the brain with PET ligand amyloid imaging is not as harmless as many thought just a few years ago, but signals emerging AD, has been a quite important advance. I agree with these valuable posts that we need to admit our lack of knowldege more when it comes to Abeta.

I thank Gunnar Gouras sincerely for his invaluable insights into the complexity that is Aβ, built over a long career doing very careful work. The complexity of “Aβ” is being more widely acknowledged as the community reflects on evidence accumulated so far. Gouras raises important points that need careful thought.


On the question of terminology – language is intimately connected with how we understand things and it is quite likely that the understanding of “Aβ” in its myriad forms and its roles in disease lacks clarity in part due to different understandings of what we mean by the term “Aβ”. Molecular biologists, physical chemists, physicians and disease modellers may connect the term Aβ with slightly different meanings  and as Gouras asks, does an imaging researcher need to know the specific molecules represented in imaging for amyloid (a collection of molecules in a particular aggregation complex) in order to do useful work? It is likely that the term “Aβ” currently does not translate between different research disciplines with the specificity required for scientific research.


Gouras further highlights the lack of clarity relating to the current use and understanding of the term Aβ – not only are the terms amyloid and Aβ used interchangeably as Gouras points out, but that for some in the dementia research community the term Aβ implicitly includes all products from γ- cleavage, including P3-type following initial α-cleavage and others e.g. Aβ’-type following initial BACE2 cleavage. Experimentally this is reflected in the use of antibodies reactive with C-terminal epitopes of Aβ(x-40) or Aβ(x-42) in a single step that are interpreted as representing Aβ40 or Aβ42 with no information relating to the N-terminal – there are many such studies in the literature. However, explicitly, this lack of clarity has not been widely acknowledged until recently. At the AAIC 2017 conference in London, of those that would discuss this issue with me, (including junior researchers, mid-career researchers and representatives from antibody companies), most had no knowledge of the antibody cross-reactivity problem and ~25% had very little basic knowledge relating to alternative products from the complex amyloid precursor protein (APP) proteolytic system. This lack of clarity has the potential to undermine research strategy, especially where results are interpreted as representing flow through sequential β- and γ- cleavage pathways when actually the single step protocol represents all products following γ- cleavage with particular C-terminals regardless of initial cleavages - with fundamental consequences for how we model disease pathways.


Lack of clarity due to terminology is an easy problem to solve. We as a community need to develop a terminology that gives clarity to the complexity of Aβ. We should specify Aβ more precisely by formally defining products from sequential β- and γ- cleavages as “Aβ” – an umbrella concept. We can then further define these products according to sequence, aggregation state etc. e.g. Aβ(N-terminal – C-terminal) x (aggregation state: monomer, oligomer, fibril). We could also do this with P3 as an umbrella concept for products from sequential α- and γ- cleavages with further detail specifying the N-terminal – C-terminal and aggregation state. Other pathways such as initial cleavage via BACE2 and cleavage products could be treated in the same way so evidence generated from investigations of the products from each cleavage pathway can be mapped with clarity. Specific formats for the reporting of genetic information have given clarity to complexity there – I suggest that the dementia research community would benefit greatly from formal reporting standards applied to all products derived from the APP proteolytic system. We can do this now.


Gouras rightly makes the point that the drive to simplify is strong. This reductionist approach is essential to experimental design across biomedical research. Although all researchers are aware that dementia is a complex and possibly wicked problem, the dominant biomedical approach of recent decades has effectively reduced complexity in Alzheimer’s disease research to measures of Aβ (and to a lesser extent tau). Does the reduction of the APP proteolytic system to measures of “Aβ” (that we know are imperfect) accurately reflect the proteolytic system we are trying to understand? When I presented my APP matrix approach (AMA) [1-4] (first rejected for publication in 2006, presented only as a poster and never invited for a talk at local, national or international conferences) at the AAIC 2011 in Paris, a major (and recurring) challenge was – How do we test this? The amyloid cascade hypothesis (ACH) allows doable biomedical questions to be easily formulated and tested whereas the AMA does not. The AMA requires a natural history “ecological” approach where careful measures of the entire system allow each fragment to be measured and controlled for – something that the ACH has not included so that evidence arising from approaches based on the ACH is confounded to an unknown extent by lack of controlling forfull length APP and other proteolytic fragments. From this point it naturally follows that we must ask the question -Is it currently possible to take the complexity of the APP proteolytic system into account experimentally and measure all the fragments, both cross-sectionally, representing levels at a single point in time, and longitudinally, to assess change? Do we have the tools to take this ecological approach forwards? Is it doable? I would suggest that we are at a point where advances in technology and data analysis are reaching a point where this approach is doable. Gouras is right to highlight that the problems I describe are from a retrospective point of view – after all, the best time to design an experiment is when all the results are in!


Gouras also rightly points out that the evidence we have for products from the APP proteolytic system may depend on which experimental models we are using. Which of the thousands of neuronal, glial, vascular and other cell types in the brain contribute to the production of the different APP proteolytic fragments, indeed which anatomical area of the brain should we be looking in? Gouras raises issues relating to the dominance of neuronal production of Aβ as opposed to P3 and the difficulties of finding P3 in the human brain. I would suggest that the evidence we have is too uncertain at this point in time as we haven’t been looking systematically.


The last points Gouras raises with respect to APP proteolytic fragments and amyloid imaging as biomarkers of AD are more problematic. Although Aβ related pathologies increase risk of dementia, we know that relationships between Aβ related neuropathological assessments and dementia status in the older population are complex and age is a significant contributor – cut offs for diagnostic categories for none, possible, probable and definite AD are age dependent [5-8]. Aβ related pathologies may contribute diagnostically but they are not themselves diagnostic for AD with certainty unless information relating to other pathologies in the brain and clinical cognitive status is known. As Gouras says, much work has been done to develop more accurate Aβ/amyloid related biomarkers whether imaging based, or from CSF or blood based molecular markers, though it should be noted that the antibody cross reactivity problem has not been fully addressed in biomarker research. Putting this problem to one side - we would expect Aβ/amyloid related biomarkers to broadly agree across the different experimental approaches, they are all measuring different perspectives of the same disease feature and in that sense the current markers can be understood as fairly robust representations of something. The problem lies in using these Aβ/amyloid related biomarkers as markers of AD specifically, rather than as markers of processes related to the APP proteolytic system. Clinical imaging for amyloid or ratios of Aβ42:Aβ40 in various biological fluids in those without clinical dementia are not themselves strictly diagnostic and no longitudinal prognostic studies combining clinical biomarkers, pathology and cognitive status have yet been completed in the older population, where most dementia occurs. Imaging and fluid based biomarkers of amyloid/Aβ most likely represent deposition in the brain however, we do not know in detail how amyloid deposition in the brain relates to dementia initiation or progression in the population and questions remain as to how useful these biomarkers are clinically.


The recent proposal to re-define AD based on presence of neuropathologies and re-define clinical AD as a combination of pathology and cognitive impairment may simplify experimental approaches in research but it does not simplify the translation of experimental evidence to the selection of useful therapeutic targets in the population. Following this biomedical approach of re-defining AD pathologically through to developing pharmacological interventions to modulate Aβ levels raises significant questions. How safe would this type of intervention be? Clearly from the perspective of the ACH where Aβ is causal, removal of Aβ is a sensible therapeutic approach. From the perspective of the AMA, we are not certain whether Aβ is the best descriptor of this system or which change in this system best relates to dementia. Is dementia related to the absolute levels of a particular fragment, ratios between several or all the fragments or even related to the coherence of the APP cleavage pathways with the wider functions of the cell? From the perspective of the AMA, dementia could be related to inappropriate changes in relative flow through the various competing cleavage pathways and full length APP. Removal of physiologically relevant forms of Aβ could relieve end product inhibition for the β-pathway, leading to increased β-cleavage and reduced α-cleavage – with unknown consequences for dementia initiation and progression. We cannot yet assume that interventions to change Aβ levels have no harmful long term consequences in those without dementia; we do not have the relevant information. Even if interventions to remove a specific form of Aβ do not cause harm or uncomfortable side-effects, given the complex relationships between dementia status and pathology, who should we treat and will societies be able to afford it?


Without a detailed epidemiological approach in the older population, we cannot be certain that we have framed the problems of AD in the most useful way – a controversial view perhaps and certainly a view that in the past has been difficult to publish in high ranking journals but a rational challenge to current amyloid/Aβ research strategy none the less.



1.            Hunter, S. and C. Brayne, Relationships between the amyloid precursor protein and its various proteolytic fragments and neuronal systems. Alzheimers Res Ther, 2012. 4(2): p. 10.

2.            Hunter, S. and C. Brayne, Integrating Data for Modeling Biological Complexity, in Springer Handbook of Bio-/Neuro-informatics, N. Kasabov, Editor. 2014, Springer-Verlag: Berlin Heidelberg. p. 921-940.

3.            Hunter, S., R.P. Friedland, and C. Brayne, 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(4): p. 254-62.

4.            Hunter, S., S. Martin, and C. Brayne, The APP Proteolytic System and Its Interactions with Dynamic Networks in Alzheimer's Disease. Methods Mol Biol, 2016. 1303: p. 71-99.

5.            Mirra, S.S., et al., The Consortium to Establish a Registry for Alzheimer's Disease (CERAD). Part II. Standardization of the neuropathologic assessment of Alzheimer's disease. Neurology, 1991. 41(4): p. 479-86.

6.            Mirra, S.S., Neuropathological assessment of Alzheimer's disease: the experience of the Consortium to Establish a Registry for Alzheimer's Disease. Int Psychogeriatr, 1997. 9 Suppl 1: p. 263-8; discussion 269-72.

7.            Hyman, B.T., et al., National Institute on Aging-Alzheimer's Association guidelines for the neuropathologic assessment of Alzheimer's disease. Alzheimers Dement, 2012. 8(1): p. 1-13.

8.            Montine, T.J., et al., National Institute on Aging-Alzheimer's Association guidelines for the neuropathologic assessment of Alzheimer's disease: a practical approach. Acta Neuropathol, 2012. 123(1): p. 1-11.

The population study by Roberts et al, (Prevalence and Outcomes of Amyloid Positivity Among Persons Without Dementia in a Longitudinal, Population-Based Setting. Roberts et al 2018 JAMA Neurol.  Published online April 30, 2018. doi:10.1001/jamaneurol.2018.0629) is of great interest. These essential population studies are now maturing to a point where reliable estimates for how amyloid-related biomarkers relate to risk of developing AD in the older population are becoming available.