At a postmortem discussion for solanezumab therapy in mild Alzheimer’s disease, held January 19 in London, members of the top echelons of AD research in the UK and other countries discussed CSF biomarker data from the Expedition 3 trial shared by scientists from Eli Lilly and company (Part 1 of this series). From there, they explored where the field should head next. Their agenda was not only to take stock of where the amyloid hypothesis stands after this latest clinical setback, but also to articulate research priorities for their meeting host, Alzheimer’s Research UK (ARUK) and for funders and the field at large. How should AD research evolve in 2017? While aducanumab, verubecestat, and other drugs are wending their way through Phase 3 (see Therapeutics database), how should translational researchers broaden their lines of attack?

In short, the researchers agreed, they should do it by integrating more information into the amyloid hypothesis. Much more information, in fact. To be sure, solanezumab has not tested the amyloid hypothesis and current trials should continue. But at the same time, the hypothesis must change. In the 25 years since its inception, it has remained too rigid, said Bart De Strooper, Dementia Research Institute, London. Drug discovery still treats it as a linear concept, ignoring evidence that AD comprises parallel, and often circular, pathways of proteostasis, lipid metabolism, and glial activation. Each of these pathways interact with Aβ and tau in ways that remain poorly defined. “It’s not always that it starts with amyloid and ends with dementia,” De Strooper said, “Aβ is not equal to AD, so we need to think much more carefully.”

Rather than a linear amyloid hypothesis, researchers are conceptualizing circular, multicausal models for Alzheimer’s pathogenesis. [Courtesy of Bart De Strooper.]

The same goes for tau. “We really need to settle what is going on between the two main pathways. In trying to depict how tau relates to Aβ we draw lots of arrows, but we do not know what the arrows are,” said Luc Buee of University of Lille, INSERM, France. At the ARUK meeting, researchers in industry and academia agreed that the field in general has been too content to draw arrows between individual areas that are themselves somewhat understood, while leaving the arrows unexplained. The challenge now is to find ways to connect pathways to one another, because the whole makes up AD pathogenesis. “How do we link areas where we have some knowledge, and fill those mechanistic gaps?” is how Mike Hutton of Eli Lilly and Company put it.

Amyloid and tau pathways need to be integrated. Much of the research effort lies in understanding what mechanisms lie behind the links currently depicted as arrows. [Courtesy of Luc Buee.]

This work can start with GWAS hits and other genetic data. John Hardy of UCL noted a current example, whereby studying co-regulated variants in genes such as Trem2 and Abi3, as well as other genes including ABCA7 and even ApoE, is surfacing a theme of insufficient repair of damage to membrane lipids subsequent to amyloid formation. This kind of research requires a tremendous amount of work, De Strooper noted. It is worth the effort because it not only explains complex events downstream of amyloid formation but may also yield druggable targets. Finding new targets outside of Aβ remains essential, as a decade or more of clinical trials of non-amyloid therapeutic approaches has been every bit as disappointing as trials of amyloid-based drugs (see non-amyloid drug trials in Therapeutics ).

Pathways derived from new genetics need to be modeled in cells and animals, preferably supported in a systematic way as is being attempted in the U.S.-based MODEL-AD initiative (see Jan 2017 news; Dec 2016 conference news). Tau needs knock-in mice, Buee said. Beyond that, one new way of humanizing mouse models is to transplant AD-derived PSC neurons into mice and study their function and deterioration over time.

Drug discovery efforts targeting Aβ may consider using new measures that are informed by mechanistic research on how presenilin mutations make the γ-secretase carboxypeptidase function less efficient. [Courtesy of Lucia Chavez-Gutierrez.]

Separately, drug discovery research could make its measures more meaningful by incorporating advances about how presenilin mutations affect APP processing. For example, the Aβ40/42 ratio is a biologically arbitrary measure. “We measure it simply because we can,” De Strooper said. An Aβ38/42 ratio would better capture the current understanding that most mutations render the γ-secretase complex’s carboxypetidase activity inefficient. 

To make oligomeric Aβ more tractable, the field should move beyond the stage where each lab has its favorite species. It could generate some consensus about the most important ones, and define those molecularly and functionally, De Strooper said. Other speakers at the ARUK meeting bemoaned how Alzheimer’s research tends to produce flashy papers and then move on to the next story. This leaves drug discovery to deal with lots of tantalizing but unsubstantiated ideas instead of producing converging evidence and tangible drug targets, said John Skidmore of ARUK’s Cambridge Drug Discovery Institute. For example, on the key question of how Aβ is neurotoxic, myriad papers proffer a list of potential therapeutic targets across receptor and membrane interactions. In practice, however, this literature suffers from "oversimplified thinking," De Strooper said, where one lab draws broad conclusions from a specific finding in a given experimental system, and too few labs replicate in a collective effort to weed out false starts and validate some central truths.

On toxicity, the sense at the ARUK roundtable was that Aβ does not directly kill neurons in AD. Why? Largely because toxicity is a slow process. The researchers agreed that structurally defining the most harmful forms of Aβ, which might only constitute a small fraction of the total, remains a priority. The path from those forms to neuronal death might be indirect, and go through tau or glia. On tau, the evidence that neurofibrillary pathology parallels regional neurodegeneration in AD is compelling. On glia, it is emerging. For example, a recent paper pegged three microglial cytokines as coaxing forth a neurotoxic subpopulation from among nurturing astrocytes (see Jan 2017 news).

Researchers emphasized that the term “neuroinflammation” is misleading in Alzheimer’s. “We should call it a different term,” said John Kemp of Janssen’s Neuroscience Discovery Europe.

Studies comparing gene expression modules show that Alzheimer’s does not cluster with bona fide inflammatory diseases, including multiple sclerosis. Likewise, CSF cytokine profiles indicate that what is going on in AD differs from what is classically thought of as neuroinflammation. Rather than framing their thinking in terms of neuroinflammation, AD researchers might be better served by delineating pathways of micro- and astrocytosis. AD-specific molecular phenotypes among glia might bear druggable targets on their surface.

In theory, tau’s complex biology offers many angles for therapy development. [Courtesy of Luc Buee.] 

As for tau, its gene is not a heavyweight in human AD genetics. Even so, the protein’s central role in Aβ neurotoxicity is undisputed thanks to research in neuropathology, CSF, disease staging, and cell and animal models. Moreover, tau PET is starting to link tangle pathology more tightly to cognitive decline than amyloid plaques. Being a microtubule-associated, but also a secreted and aggregating protein that is made in numerous splice variants, tau’s complex biology theoretically offers numerous flanks for attack by therapies. Alas, tau has been an elusive target.

Despite much effort in pharma companies and academic labs, no safe and effective drugs to inhibit tau’s hyperphosphorylation have been found. Few even made it to clinical trials. Indeed, biopsy studies have made clear that certain kinds of tau phosphorylation are physiological and lost postmortem (see Nov 2016 news). “We have to be very careful which phosphorylated tau we target therapeutically,” Buee said.

These different approaches to drug development for tauopathy are in different stages, from preclinical development to clinical trials. [Courtesy of Luc Buee.]

The first clinical trials of drugs targeting tau have failed (see Therapeutics database) and the Phase 3 aggregation inhibitor LMTM is widely seen to have been negative, as well (see Dec 2016 conference news). As of early 2017, tau immunotherapies are showing some promise in the clinic, though Buee cautioned that it’s early days, and characterization of their targets is limited (see Therapeutics).

As a field, Alzheimer’s research has produced fewer druggable targets than other disease areas, said Skidmore. That is true at least of classical targets such as enzymes and receptors. Take ApoE, or the high-profile area of protein propagation, which describes anatomical spread qualitatively but does not show toxicity, or generate handles for drug discovery. “We need to learn how to tackle classically un-druggable targets such as protein-protein interactions,” Skidmore said. Paul Whiting, of the ARUK Drug Discovery Institute at UCL, suggested that AD research advance from an era where it relied on pathologists and geneticists to a future of mechanistic and quantitative models. To this end, researchers urged AD funders to attract engineers, lipid biologists, and immunologists, and to fund them for a sufficiently long period so they can make their mark in a new field.

After years of research, the immediate causes of dementia remain mysterious, scientists conceded. Different levels of investigation, with their wildly different tools and languages, are each advancing on their own, but have not yet linked up a upstream cause—say, accumulated Aβ or tau—to the erosion of memory and function people experience as disease. Is it synaptotoxicity? Neuronal cell death? Glial activation? Circuit degradation? To solve this old question, scientists at the London roundtable argued for focusing resources on the convergent finding that it takes 15 years from amyloid to dementia, or indeed from a pretangle to a ghost tangle. This long period of enormous homeostasis of the brain should be characterized with systematic, genome-wide and cell-wide approaches. “I am dreaming of an atlas of AD, where we see how expression of twenty thousand genes in 100 different cell types evolves over time, Hardy said.

In addition, the group recommended to AD funders and leaders that they prioritize these areas:

  • Stay the course with approaches being taken at the moment. Science is learning a lot.
  • In parallel, support work that uses genetics to define new pathways.
  • To supporting pathway analysis, remove obstacles to public availability of genetic data.
  • Use genetics to strengthen clinical trials, e.g. by developing risk scores that boost the predictive value of ApoE and help identify at-risk participants for early stage trials.
  • Support ongoing clinical trials: speed recruitment, unify registries, improve retention.
  • Support development and validation of more sensitive readouts that can become surrogates for clinical benefit, e.g., wearable technologies, digital apps, home-based activity monitoring or cognitive testing. Better tools can help sponsors make better decisions before entering Phase 3.
  • Build biomarkers into trials across drugs and sponsors. Enable biomarker data from across trials to be analyzed together in such a way that the best markers are being iteratively validated for use by all sponsors. Foster the organizational cooperation needed to achieve that. In analogy, genetics started out with small, irreproducible signals, but generated meaningful results once large sample collections were pooled.
  • Improve education about translational research and clinical trials. Fund university courses that teach how to advance basic science to clinical trials. Educate journal editors to aid selection of rigorous clinical trial manuscripts; educate the public about the importance of trial participation. Foster contact between scientists and patients.

There is much to do to put therapy development for Alzheimer’s on a stronger footing, the roundtable agreed. Lest ideas drift apart, however, they concluded with a reminder of what unites them. Alzheimer’s research in 2017 suggests this broad umbrella is probably true: Everyone develops some tau pathology as they age; some people also develop amyloid pathology; in them, tau pathology spreads and prompts a microglial and astrocytic response; this leads to Alzheimer’s dementia. Vascular, metabolic, and other factors impinge. “Let’s not overcomplicate. This basic thinking frame remains useful,” Janssen’s Kemp concluded.—Gabrielle Strobel

Comments

  1. Unfortunately, parallel worlds exist that Alzforum does not refer to. We all have our examples. Mine are exemplified by Clark and Vissel, 2015

    References:

    . Amyloid β: one of three danger-associated molecules that are secondary inducers of the proinflammatory cytokines that mediate Alzheimer's disease. Br J Pharmacol. 2015 Aug;172(15):3714-27. Epub 2015 Jun 29 PubMed.

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References

Therapeutics Citations

  1. Solanezumab
  2. Aducanumab
  3. Verubecestat

News Citations

  1. Building Better Mouse Models for Late-Onset Alzheimer’s
  2. Next-Generation Mouse Models: Tau Knock-ins and Human Chimeras
  3. Microglia Give Astrocytes License to Kill
  4. Is Tau Phosphorylation All Bad?
  5. Tau Inhibitor Fails Again—Subgroup Analysis Irks Clinicians at CTAD

Other Citations

  1. Part 1

Further Reading

No Available Further Reading