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DBL%20Hendrix%20small.png College chemistry, 1983

Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: derekb.lowe@gmail.com Twitter: Dereklowe

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January 9, 2014

An All-In-One Alzheimer's Paper

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Posted by Derek

A reader sent along this paper that's come out recently in JACS, from a Michigan/South Korea/UCSB team of researchers. It's directed towards a possible therapeutic agent for Alzheimer's disease. They're attempting to build a molecule that binds beta-amyloid, coordinates metals, and has antioxidant properties all at the same time.

An uncharitable view would be that they have also taken aim at the year 1995, which is about when all three of these ideas were also being worked on for AD. But it's not like the field has cleared up too many of these questions since then, so perhaps that gets a pass, although it should be noted (but isn't in the paper) that no one has ever been able to find any significant effect on Alzheimer's from treatment with either antioxidants or metal chelators. The debate on whether anyone has been able to see anything significant with agents targeting amyloid is still going on (and how).

I bring that up partly for mechanistic plausibility, and partly because of the all-in-one aspect of the molecule that the paper is studying. Any such drug candidate has to justify its existence versus a mixture of therapies given simultaneously, especially since the odds are that it will not be as efficacious against all (or even any) of its subtargets compared to a cocktail of more specific agents. With Alzheimer's, it's tempting to say that well, we're hitting all three of these mechanisms at once, so that has to be a good thing. But are all three of them equally important? The fraction of your compound that's binding amyloid is presumably not available to serve as an antioxidant. The ones that have chelated metals are not available to bind amyloid, and so on.

Most of the paper details experiments to show that the ligand does indeed bind amyloid, both in the soluble form and as fibrils. But there's room to argue there, too. Some in the field think that altering the distribution between those populations could be important (I'm agnostic on this point, as I am about amyloid in general). If you're binding to all of them, though, what happens? There's information on the compound's effect on amyloid oligomerization, but the connection between that and Alzheimer's pathology is also up for argument. These questions, already complicated, are made harder to think about by the absence of any quantitative binding data in the paper - at least, if it's there, I'm not seeing it yet. There are mass spec, LC, and NMR experiments, but no binding constants.

There's also little or no SAR. You'd almost get the impression that this was the first and only compound made and tested, because there's nothing in the main body of the paper about any analogs, other than a comparison to a single quinolinemethanol. Even without binding data, some qualitative comparisons might have been made to see how the amyloid binding responded to changes in the structure, as well as how it balanced with the metal-binding and antioxidant properties.

There's some cell-assay data, viability in the presence of amyloid (with and without metals), and it looks like under A-beta-42 conditions the cells are about 70% viable without the compound, and around 90% with it. (It also looks like the cell viability is only in the lower 80% range just when the compound alone is added; I don't know what the background viability numbers are, because that control doesn't seem to be in there). They also tried the same neuroblastoma line with the Swedish-mutation APP in it (a huge risk factor for an early-onset form of human Alzheimer's), but I can't see much difference in the compound's effects.

But as with any CNS proposal, the big question is "Does the compound get into the brain?" The authors, to their credit, do have some data here, but it's puzzlingly incomplete. They show plasma and brain levels after oral gavage (10 mpk) in CD1 mice, but only at one time point, five minutes. That seems mighty early for an oral dose, at least to me, and you really, really want to see a curve here rather than one early time point. For what it's worth, plasma levels were around 6 ng/g and brain levels were around 14 ng/g at that point, but since this was just done by brain homogenate, it's unclear if the compound really gets in or not. No other tissues were examined.

There also don't seem to be any data on what else this compound might do. If you're seriously proposing it as a possible therapy for Alzheimer's, or as a starting point for one, it would be worthwhile to collect some numbers in selectivity screens. Alternatively, if you're not proposing this as a starting point for Alzheimer's therapy, then why do all this work in the first place (and why write it up for JACS)? This is another one of those cases where I'm honestly baffled by what I'm reading. My industrial perspective sees a single compound given a very labor-intensive in vitro workup on a hazy therapeutic rationale, with no analogs, no selectivity data, and no PK other than one time point, and I just shrug my shoulders with a puzzled look on my face. Why do it?

Well, universities aren't drug companies. And the groups involved are, presumably, not focused on making the next big Alzheimer's breakthrough. But what are they focused on? Training students? That's a really worthwhile goal, but I have to wonder if some way could have been found to train them that would have been a bit more congruent with the real world. Picking three rationales, thinking up a single compound to try to combine them, and then spending all your effort on it as if it's a real lead isn't (to my mind) a good fit. I realize that resources are limited, and that this same level of effort just couldn't have been applied to a whole series of compounds the way it would in an industrial setting (not that we'd have done it). But if you're going to do this stuff, a less-intense look at the amyloid-aggregating and cellular effects of a wider series of compounds could have been more valuable than a lot of information about just one.

I feel bad every time I write like this about academic drug-discovery papers, but I can't help it. From my perspective, there's a lot of confusion out there about what drug discovery really entails, and about the relative value of doing a little of it, or doing it in an odd way.

Comments (55) + TrackBacks (0) | Category: Academia (vs. Industry) | Alzheimer's Disease


COMMENTS

1. UIC Alchemist on January 9, 2014 10:08 AM writes...

At the very least its a nice looking TOC graphic

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2. annon too on January 9, 2014 10:14 AM writes...

Hey, it's a good looking publication that will help students get jobs & the primary investigator get more grant money. Isn't that what it is all about?

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3. The Fat Layer on January 9, 2014 10:19 AM writes...

"Well, universities aren't drug companies."

I agree. In my view, even though many universities claim to have "drug discovery" initiatives, the fact that they work mainly under an academic environment where their efforts and funding comes from grants, in really they work and focus on basic research.

By basic research I mean trying new things for the sake of learn more about the problem at hand, but not necessarily using parameters that will turn such studies and results into products.

In my humble opinion, that's where the disconnect exists.

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4. passionlessDrone on January 9, 2014 10:25 AM writes...

Err. Peroxinates or whatever compound every time AZ comes up on this blog.

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5. David Formerly Known as a Chemist on January 9, 2014 10:34 AM writes...

Academic research focuses on what has been funded, or what the PI thinks he/she can get funded and published. No deeper analysis of "why do it?" is necessary.

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6. Anon on January 9, 2014 10:35 AM writes...

What about the idea that someone might pick up this compound as a starting point for further and more thorough development? That's what academic "drug discovery" efforts should really have as their ultimate goal. In a way, that is a form of basic research.

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7. BTDT on January 9, 2014 10:36 AM writes...

My opinion for what it's worth - The only realistic way that academia can successfully do small molecule drug discovery is to have a PI (or co-PI) with substantial industry med chem experience.

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8. petros on January 9, 2014 10:42 AM writes...

Is JACS the appropriate journal for such a paper?

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9. Puff the Mutant Dragon on January 9, 2014 11:01 AM writes...

This paper is useless, but I have to agree with (1) -- I like the picture, that graphic is worth more than the paper.

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10. David Borhani on January 9, 2014 11:08 AM writes...

Typical of such academic dreck, there are no dose-response experiments.

And as long as we're thinking along the lines of this group, why not just do a clinical trial to test the effect of o-phenanthroline?

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11. Chemjobber on January 9, 2014 11:41 AM writes...

To paraphrase the driver at the beginning of "The Untouchables", "It ain't supposed to be good! It's supposed to be published."

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12. RTW on January 9, 2014 12:40 PM writes...

@7.BTDT - The University of Michigan has quite a few people in the Pharmacy and Med Chem departments that have industry experience. Some with nearly 30 years in industry, and marketed drugs to their credit. I doubt this paper was circulated to any of them to review prior to being sent in for publication. JACS might have accepted it because of its potential idea of combining several approaches. MedChem journals likely would have asked that more work be done to answer some of the same questions Derek raised.

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13. Vasili on January 9, 2014 1:39 PM writes...

Where is Lane Simonian?

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14. anon the II on January 9, 2014 1:58 PM writes...

This work should never have been done and JACS should never have published it. The reviewers should be flogged. In private, of course, since it was reviewed confidentially. But flogged, just the same.

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15. Ty on January 9, 2014 2:05 PM writes...

"It also looks like the cell viability is only in the lower 80% range just when the compound alone is added; I don't know what the background viability numbers are, because that control doesn't seem to be in there"

They normalize those to the untreated control, which is set at 100%.

For the cocktail vs. single drug approach, you could make the argument that now you only have to worry about one drug getting across the BBB, rather than all components of the cocktail. However, claiming multiple functionalities bothers me from a basic science perspective, since once you switch to in vitro and in vivo experiments, it's really tough to know what's going on because it's harder to control the variables (but then again, this is coming from the grad student/postdoc academic perspective).

The comments are coming across way too harsh here, I think. There are problems with the paper (I agree about the dose response and binding constant), but I didn't read it and think "this is trash." I think the industry guys are being a bit tough.

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16. Rafael Najmanovich on January 9, 2014 2:31 PM writes...

The note above can be broken down into:

1. valid criticism of the article: the work is incomplete without dose responses, time courses, etc.

2. valid but open questions about the work: is it worth to pursue such a polypharmacologic approach?, are any of the targeted mechanisms proven?, etc.

it is a case of perhaps the authors overselling what they did, after all it could at most only be a research inhibitor (not even a lead compound yet). Now, for the rest of Derek's comments and many of the blind followers, to completely dismiss any role for academic research in drug design is naive and counterproductive. As has been plenty discussed by people like Aled Edwards from the SGC, hundreds of potential targets lay untouched by industry until the day that an academic paper proves it may be useful and in many cases these papers come up with a research inhibitor that serves to guide future development. Second, industry (well management at least) itself is starting to turn towards academia for more and more of the earlier and riskier stages of drug design and see the worth in fomenting such interactions.

So yes, for any number of potential reasons the paper is incomplete but as long as the methodology is correct and the conclusions are based on the data it has merit - If it doesn't help anyone to get closer to find a cure to a disease, so be it. It will not be the first nor the last such research be it in academia or industry.

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17. MoMo on January 9, 2014 2:42 PM writes...

I smell weakness from the Pharma comments! Face it, you all have even less to show for the billions poured into anti-AZ compounds and research.

This paper highlights just one compound out of many that were the subject of patent published last June and shows that a multifunctional compound against AZ can be designed and made to work on many levels and mechanisms.

But that is the problem with Industry- you all think its just one target or mechanism that is the cause of AZ, when, in fact, its multifactorial.

Don't let this bother you Dr. Lim!

Its only a Blog and the Internet, frequented by frustrated and increasingly unemployed scientists!

Let the Big Clear Out continue!

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18. eugene on January 9, 2014 2:47 PM writes...

"I think the industry guys are being a bit tough."

Not really. I'm afraid of getting Alzheimer's and having to kill myself when I'm old before I lose my mind, and these studies that waste time and valuable resources come out, I'm not going to penalize anyone for not being 'civil' enough.

Another pet peeve of mine in the area are the 'organometallic' approaches for binding amyloid, where the 'organometallic' probably will not make it past the BBB and the dose required will kill you. Well, actually... that type of cure for Alzheimer's will be fine for me in the absence of anything effective, which is likely what will happen if the NIH keeps wasting its money on poorly thought out things.

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19. eugene on January 9, 2014 2:56 PM writes...

"Now, for the rest of Derek's comments and many of the blind followers, to completely dismiss any role for academic research in drug design is naive and counterproductive."

Ridiculous. No one is dismissing academic research in drug discovery. I'm just dismissing a simplistic, overhyped approach to a complex problem. Despite my comment above, I know someone who is synthesizing corrole organometallics as drug candidates. But that person is really careful and does not make sensationalist claims and they try to get industry partners as well as conduct extensive toxicity studies.

How come you don't realize that most of us were in academia at one time, and a lot of Derek's 'followers' are still there? I don't see this as an 'academia' vs. 'industry' thing. NIH money should go to those academic groups who have a realistic perspective of how drug discovery works and that don't make sensationalist claims.

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20. Bob on January 9, 2014 3:40 PM writes...

@ #18, 19. The paper only uses the word drug once, in the context of including "drug-likeness" as a designed property, and therapeutics once in the conclusion, "In our future efforts, we intend to extend this work and build a foundation toward the development of *chemical tools for uncovering complex AD pathogenesis that will form the basis for the discovery of effective therapeutics for this disease*." They claim they are making probes, that may one day be turned into something of a drug. All the "hype" comes from Derek, not the paper.

A paper on the development of a multifaceted probe should not be crapped on for not being a drug discovery paper since that clearly wasn't the goal. Not to mention, how amyloids cause amyloid-associated diseases is still a very open question. I, for one, think studying this is still completely worth spending basic science grant money on. There is also a multipurpose small molecule design bent to it as well that is worthwhile from a basic science angle.

These comments make me think all the industry outsourcing has less to do with money and more to do with being on a different continent than industry scientists.

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21. JSR on January 9, 2014 5:40 PM writes...

The problem with this paper starts with its title:

Rational Design of a Structural Framework with Potential Use to Develop Chemical Reagents That Target and Modulate Multiple Facets of Alzheimer’s Disease

If the end result of months or years of work by 14 authors and almost as many sources of funding is a "design" of a "framework" that could maybe be used to "develop ... reagents" that may only "target" or "modulate" "facets" of AD, you're not ready to publish, especially not in the once hallowed pages of JACS.

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22. gippgig on January 9, 2014 5:52 PM writes...

"...there's a lot of confusion out there about what drug discovery really entails..."
Has anyone written a how-to manual for those outside the industry who want to give it a try?

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23. MB on January 9, 2014 7:01 PM writes...

I do a bit of drug discovery in an academic setting. The reason why it is so different than industry is because we often have vastly limited resources and personnel compared to industry as well as limited amounts of time. Si you'd like to get PK data? Ha! Yeah right. You'll have to spend the next 6 months or so just trying to find a lab with the right mass spec equipment that will also let you use it. Want analogs? Too bad, you're the only person that is available to mane them. Not only that, you have to do all the biology yourself as well. I'd love to do screening, analoging, and in vivo testing, unfortunately academia is a massive bureaucracy where it takes forever to get things done. Let's not also forget we are working with extremely limited budgets. I'm basically an entire drug discovery program rolled into one person.

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24. MB on January 9, 2014 7:02 PM writes...

I do a bit of drug discovery in an academic setting. The reason why it is so different than industry is because we often have vastly limited resources and personnel compared to industry as well as limited amounts of time. Si you'd like to get PK data? Ha! Yeah right. You'll have to spend the next 6 months or so just trying to find a lab with the right mass spec equipment that will also let you use it. Want analogs? Too bad, you're the only person that is available to make them. Not only that, you have to do all the biology yourself as well. I'd love to do screening, analoging, and in vivo testing, unfortunately academia is a massive bureaucracy where it takes forever to get things done. Let's not also forget we are working with extremely limited budgets. I'm basically an entire drug discovery program rolled into one person.

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25. Lane Simonian on January 9, 2014 7:46 PM writes...

I am here, just temporarily a day ahead of most of you.

I believe these researchers have identified the correct approach to treating Alzheimer's disease. Oxidation, metal ions, and amyloid plaques or oligomers are all involved in Alzheimer's disease--in that order of importance (the most important being oxidation). All three are interrelated so attacking one reduces the other two.

Initially amyloid attracts copper and zinc increasing the conversion of superoxide anions into hdyrogen peroxide. Peroxynitrite scavengers convert peroxynitrites into a nitrite anion and water (ONOO- + 2h+ 2e-=H20 + NO2-). The nitrite anion combines with hdyrogen peroxide to reform peroxynitrites (H202 + N02-=ONOO- + H20). Copper and zinc may also play a role in amyloid aggregation and nitration (either mediated by peroxynitrites or iron ions) may play a role as well. So if you chelate certain metal ions early, you may lower levels of amyloid plaques and peroxynitrites. Certain phenolic compounds also inhibit part of the pathway via protein kinase C that leads both to peroxynitrites and the processing of the amyloid precursor protein.

As the disease progresses, copper and zinc are enotombed in amyloid plaques and more superoxide is available to combine with inducible nitric oxide to form peroxynitrites. So perhaps, metal chelation may be positive at this point as well.

Methoxyphenols such as curcumin, ferulic acid, and eugenol are metal chelators, reduce the formation of amyloid plaques, and act as peroxynitrite scavengers. They have produced successful results in small-scale human clinical trials for mild to moderately severe Alzheimer's disease including improvements in cognition and in some cases behavior. The following discusses the multiple effects of curcumin:

The effect of curcumin (turmeric) on Alzheimer's disease: An overview

Shrikant Mishra and Kalpana Palanivelu

Abstract
This paper discusses the effects of curcumin on patients with Alzheimer's disease (AD). Curcumin (Turmeric), an ancient Indian herb used in curry powder, has been extensively studied in modern medicine and Indian systems of medicine for the treatment of various medical conditions, including cystic fibrosis, haemorrhoids, gastric ulcer, colon cancer, breast cancer, atherosclerosis, liver diseases and arthritis. It has been used in various types of treatments for dementia and traumatic brain injury. Curcumin also has a potential role in the prevention and treatment of AD. Curcumin as an antioxidant, anti-inflammatory and lipophilic action improves the cognitive functions in patients with AD. A growing body of evidence indicates that oxidative stress, free radicals, beta amyloid, cerebral deregulation caused by bio-metal toxicity and abnormal inflammatory reactions contribute to the key event in Alzheimer's disease pathology. Due to various effects of curcumin, such as decreased Beta-amyloid plaques, delayed degradation of neurons, metal-chelation, anti-inflammatory, antioxidant and decreased microglia formation, the overall memory in patients with AD has improved. This paper reviews the various mechanisms of actions of curcumin in AD and pathology.

So in a way these researchers are not suggesting anything new, just a valuable approach which would be wise to follow.

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26. Rational thinker on January 9, 2014 7:48 PM writes...

Well I do know for a fact that at least one of the main authors of this paper does have a very real, very real world reason for doing such research. Yes the data and idea behind the research is quite preliminary, I don't think that they are denying that anywhere in the paper. The reason it was published was to initiate a new direction to head in research on AD that they do thing is promising by combining a focus in these three things.

I want to agree, yes academic research and industry research is from two very different perspectives. I'm not a university researcher nor an I an industrialist either. I'm just an educated person with a background in neurophychopharmacology with a real world interest in finding anything that will help solve any of the problems at all surrounding AD, both today and yes, also down the road in the future, as we all should wether or not everyone has quite such a personal reason for doing so as I or as the writer previously mentioned; I'm an independent commentor so to speak. I'm not in the study nor do I have my own research in Industry either.

That said, I'm not so sure criticizing the way academics do their research is the direction that industrialists should go. I often find myself defending drug companies to people who complain about way to high prices of drugs (these fees don't just pay for that substance to be produced and sold, they must recoup money they spent over the years developing, testing, FDA testing for a decade, and also fund new research, it's expensive), that drugs for smaller less popular diseases are left undeveloped (drug companies are at the mercy of the free market, they can't spend all of their money on drugs for something that only affects a few, yes those people need help too but sadly when you have the market being lead by profits of coarse big ticket drugs are going to be their focus. They still work on less profitable drugs and less well known diseases but they have to think of shareholders and profits when making drugs because if the drug companies all go out of business we, and those suffering from less elegant diseases too, will have no new drugs anyway; it would be worse if their wasn't any drug research), and that drug companies do not care about the people actually taking the drugs they only care about the profit (while to some degree true, their job is not to care about the people suffering, that is friends and relatives jobs, their job is to provide effective drugs at a competitive market rate for people needing them. We should prefer them to do their jobs effectively no spend their time crying at the bedsides of those suffering; their job is not to care it is to research).

That said, for every every complaint made about how academic research is done and how they choose to spend their money from grants, there are quite literally, thousands of complaints of how industrial pharma research is done. Basically, academia is there to pick up the slack of industry to some degree. Illnesses and drugs that are left behind by the financial aspects of the drug industry, no matter the valid reason, are able to be picked up and looked at by academics who are not necessarily expected to make a profit from their research. Basically, they are able to delve into research that is from a different direction and perhaps from a more purely intellectually valuable place. That also said, nobody is going to be able to keep funding a project that is going nowhere and is of no value to anyone. They must have what someone sees as a valid idea with promise to lead to something. No erase archer with a future is going to waste his time on something if it is not going to help him, or help anyone. While they are not at the mercy of the free market to the same degree, academia is still populated by individuals with goals and a desire to get their own name, research, and product (even a more intellectual product) out there. These people are still trying to achieve something and not going to spend their time on a money pit either. This specific paper was toward the beginning of the initiative. They were using their initial ideas and results, yes I'm sure there are still questions to be asked, aspects that still need to be looked at, but it was proposing a novel way of perhaps tackling the problem.

To the commentor that suggests that the reviewers should be "flogged," wether you are graciously willing to let them be flogged in private or not, you should be ashamed of yourself. Really, you should be. I hope that you redden with shame like the child that you must be to propose such a very childish thing. Is that the type of people who are in charge in industry? Have I been mistaken all these times that I have defended drug companies to people with perhaps not as good of an understanding as myself to how both industrial and academis research is done? If I have I'm going to have to rethink my position. If you really think that someone who is simply proposing a new way to look at a research approach that is not to your personal liking should be physically spanked I'm really not sure you are in the right field or perhaps even old enough to be in the field to begin with. Perhaps you should take up something that is a little more dogmatic. Maybe you could become a parochial school teacher? Oh, my apologies to the new Catholic Church, it turns out your ideas for flogging and spanking have even become to antiquated for them...maybe a North Korean school teacher....(I think I would like to see u publicly shamed a little bit)

Anyways, this blog makes me sad. I would like to see some comments back from those who worked on the project. Yes some of their criticisms in the original blog should be addressed, I'm sure the researchers could address some of them and more research into the area could be helpful in filling in the initial holes. But that is what the original paper was trying to do, suggest a novel way of attacking (intellectually, I guess I should be more specific since readers of this can be so easy to jump to suggesting to physically flogging, privately or not) Alzheimer's research. I for one am glad there is academic researchers that are not as constrained by profits and earnings and who are also willing to look at the problem from a novel perspective. I thought that the original paper had quite a bit of promise, while new and ultimately not proven effective to the top degree, the idea of one substance doing all three sounds quite interesting and promising. We also should remember that these researchers aren't just silly students who don't know all that much about the area of Alzheimer's (the writer of the blog admits he doesn't have that much to do with the amyloid research behind this idea, one of the authors at least I know is in that specific area of the field, I've seen his name on many many papers on amyloid research, he must know quite a bit about it at least). The researchers who are doing the work and writing the papers are also doctorate holders in the field who have been studying the topic and publishing for years. It is not simply an academic topic proposed and studied as a way to train students to think outside of some box, they are also serious researchers that are taking a new idea and trying to propose we look at a topic they also know quite a lot about and go about it a new way.

Sorry so long, I just thought we should stop a minute and try to think rationally about how they may not be coming from such an industrial view but the value of an academic view and how differing perspectives are really the lifeblood of scientific research. Without them we would still be lost in the woods, probably using stripped tree branches to flog each other for proposing a new direction to head in after being stuck in said woods for so many millennia.

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27. MoMo on January 9, 2014 10:50 PM writes...

Long but good response to the industrial elitists Rational Thinker. The Pharma crowd is a bit tense these days as the axe is sharpened and falls.

Critique is easy, true work is too hard for many in Pharma, and many leaders are anything but.

Read the patent, read the paper, and you'll all realize you are wrong on this. Did I just not read here that there are no rules?

Such fine papers like this make the highly paid nervous.

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28. MoMo on January 9, 2014 10:50 PM writes...

Long but good response to the industrial elitists Rational Thinker. The Pharma crowd is a bit tense these days as the axe is sharpened and falls.

Critique is easy, true work is too hard for many in Pharma, and many leaders are anything but.

Read the patent, read the paper, and you'll all realize you are wrong on this. Did I just not read here that there are no rules?

Such fine papers like this make the highly paid nervous.

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29. MB on January 9, 2014 11:44 PM writes...

I'd also like to add that I'm a former industrial researcher myself that is currently working in an academic setting. Elitists in industry really need to get over their massive egos. If industry was so great and successful, whys is your ROI only 5% (according to another article Derek wrote) for the billions of dollars you spend? Let's not also forget the constant whining industrial researchers constantly post about the stability of their jobs or jobs losses on these reader responses. Although academia has its drawbacks, the one thing academia does NOT reject are ideas. I can do anything I absolutely want to in academia. Oh, so your molecule only has micromolar or millimolar potency? Who cares? Go ahead and pursue in vivo if you want to see if it has efficacy as long as you're willing to put in the work. In industry, however, you have to abide by insanely stupid rules to advance compounds further. No nanomolar potency? Might as well throw it in the trash. Guess what, if we listened to industry, we'd never have most of our alkylating agents to treat cancer, no hormonal agent chemotherapuetics, thalidamide would never be in clinical trials, and valproic acid (which has only millimolar efficacy for HDAC inhbition in invitro screenign) would have been thrown in the away a long time ago, and for what? All because those compounds didn't show nanomolar activity in preclinical screening, which is supposed to be some sort of prediction of potential clinical toxicity? Yet here we are, where industry has wasted billions of dollars on COX-2 inhibitors failures, for example, even though the compounds that were advanced had nanomolar potency.

I've seen both sides of the aisle and I understand where both are coming from. At least in academia we don't have to answer to stock holders and novel ideas are never rejected. Risk is something industry hates, which is why they are constantly stuck doing their stupidly conservative assays and constantly must abide by conservative and flat out arrogant rules that need to be adhered to in order advance new compounds. Which industry again has been one of the worst for job losses over the past decade?

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30. MB on January 9, 2014 11:54 PM writes...

Apologize also for the all the typos in my posts. I'm working from a smart phone.

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31. Chemist Turned Banker on January 10, 2014 2:50 AM writes...

#29 and others. I certainly would not seek to side with industry over academia (AZN's R&D productivity says all you need to know), but you are missing a major point- if industry, with its near-unlimited resources can't make a decent fist of drug discovery, why on earth do you expect a PI and a few enthusiastic postdocs to triumph so easily?

Academia has an enormous amount to offer drug discovery by offering mechanistic elucidation, tools (diagnostic or synthetic, for instance) and other insights, but soup-to-nuts drug discovery is not one of them. Imagine the reaction if a world-class aeronautical engineering department decided to start building fighter jets?

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32. Bahbah on January 10, 2014 7:59 AM writes...

Oh will you drop the ridiculous anti-academic bias you have? Without academia you wouldn't be anywhere. Industry has appalling succes rates as it is already anyway, not to mention the extraordinarily dubious marketing practices....

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33. The Iron Chemist on January 10, 2014 9:21 AM writes...

@29: You claim that academic chemistry doesn't reject ideas and that its researchers have the latitude to study anything they want. I take it that you haven't submitted a grant proposal recently?

As Lane mentioned, the authors have drawn up an interesting approach to treating AD. I think that that, rather than putting forward a compound ready for phase III testing, was the purpose of the manuscript. The latter, which seems to be the standard desired by previous commentators, is certainly unrealistic.

As I can tell you from first-hand experience, it's nearly impossible for most researchers to publish a paper in JACS that simply outlines a novel and interesting approach to addressing a particular problem. Right or wrong, referees and editors want to see some sort of application in biology. Given that the relevant parties commonly have degrees in chemistry rather than biology, a half-baked experiment often meets the requirement. I'm not saying this is the right way to do things; to the contrary, I feel that pure basic science "approach" manuscripts should be more readily accepted as they are. Regrettably, this is the game that everyone involved with these higher-profile journals has apparently decided to play.

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34. Erebus on January 10, 2014 9:35 AM writes...

They researchers may have drawn up an "interesting approach", but the study just seems too light on useful data. The paper -- pretty graphic notwithstanding -- was a very slipshod way to present that approach.

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35. SAR Screener on January 10, 2014 9:59 AM writes...

"7. BTDT on January 9, 2014 10:36 AM writes...

My opinion for what it's worth - The only realistic way that academia can successfully do small molecule drug discovery is to have a PI (or co-PI) with substantial industry med chem experience."

I’d add ‘who partners with someone who knows how to build / run relevent screening assays.’

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36. Artemisinin on January 10, 2014 10:03 AM writes...

I think the academic people are way to defensive. True, you have limited resources and etc. But what Derek pointed out are the basics that should have been covered...

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37. SamZ on January 10, 2014 10:07 AM writes...

First, I'll say I haven't read the paper, so I'm just writing to respond to the blog post and some of the comments.

re: binding constants and DR, this is just a guess, but you can't really do them reliably on polymer aggregates, like amyloid (assuming that really is the target in vivo).

re: the comments, what MB said, and a few others. I've worked on both sides. Academic labs simply don't have the resources to test lots of drugs. Even if you can test them in vitro, there's not enough money to do large scale animal studies and PK is not typically available for a reasonable price.

Also, mice are a terrible model for human disease, especially things like this. I've said it before, I'll keep saying it.

re: publishing, when the goal is proof of concept for a mechanistic hypothesis, and it sounds like it is here, it's usually best to tell a complete story and keep it simple. If they had 3 compounds, for example, they would have to address all the disparate results and have explanations for all of them. This becomes more relevant the more biology you want to do. Reviewers really don't like loose ends and studies that raise more questions than they answer. It's sad, but it's reality.

Having said that, I'm going to see if I can access the paper, seeing as how I'm currently "between jobs".

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38. SamZ on January 10, 2014 10:22 AM writes...

Ok, having looked over the paper... I see where some of the comments are coming from. I think they sent it to JACS because so much of the paper is about the synthesis?

FWIW, the cell viability assay could be an underestimate. 20-40% cell death is not nothing. But having said that, MTT assays are sort of meaningless because they lack sensitivity. Background cell death is typically ~5% in a happy cell population. The way they did the normalization is fine. But P values of

I don't know why anybody still uses MTT assays, except they're easy and cheap for HTS, and people don't seem to know any better. ROS assays on cells are also notoriously variable.

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39. SamZ on January 10, 2014 10:24 AM writes...

2nd try since a chunk out of the middle is missing?

I was saying, P values of

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40. Hap on January 10, 2014 10:27 AM writes...

Academia is supposed to be about interesting ideas with some implementation; however, just like any new idea, you want the implementation to be thought out and clear. You would also want the idea to account for what people have done previously in the area of research.

The problem is that there seem to be pieces of data that are either not there or incomplete that people would need to evaluate the idea. It seems like, for example, you'd really want selectivity data - either it will be useful as a tool compound or as a drug lead, and in either case, you would want selectivity data to validate that. (You might also want ex vivo data on the compound's binding to targets, in particular Abeta). If you think it's a potential lead, then PK data (particularly brain concentration data at more than one time point) would be helpful. I wouldn't think you'd need SAR or in-depth metabolism or PK data, so long as you could show that your compound did what you said (and preferably how well). Even if you can't tinker with the compound, if it works, you could probably use it to interrogate ideas on how AD works. Without that kind of data, though, it's hard to use the compound for anything.

New ideas aren't good because they're novel, but because they might do something. If you haven't tested your ideas enough to know that well, then it will be hard for other people to know how seriously to take the idea, both because it hasn't been tested enough, and because if you didn't test it hard enough, they might wonder what else you haven't thought of.

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41. SamZ on January 10, 2014 10:29 AM writes...

haha, you might want to upgrade to something that can parse text without assuming a symbol is an HTML tag? maybe it could default to putting comments in quotes for us?

sigh. 3rd try on that sentence.

P values of LESS THAN 0.05 for SEM of cell viability is not significant. The better way to do this is to count more cells. Real differences should be easily LESS THAN 0.01 for SEM, for ANOVA.

If JACS had better reviewers for the biology portion of this paper, someone should have questioned that section, since it's critical to their conclusions.

ok that's all.

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42. Julien Hanson on January 10, 2014 11:32 AM writes...

Dear M. Lowe,

I like your blog where I read interesting entry from time to time. Sure, you have a lot of med chem experience and valuable thought. Nevertheless, this comparison between academia vs industry sounded strange to me, based on one paper and one team. I did my PhD in an academic lab that brought a successful drug into marked without help from industry before the clinical stage and I know research conducted in industry that are unprofessional and laughable. Maybe they are just less publicised by papers and thus nobody ever heard about? Why not just commenting the science without looking from where it comes from? The problem here is not industry vs academia but an approach vs another that should be discussed solely on the science. Why rejecting an idea that looks strange from your perspective? Industry have more rules (do and don't) than academia and probably the current lack of innovation comes partly from that.

the greatest obstacle to discovery is not ignorance - it is the illusion of knowledge

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43. JR Brender on January 10, 2014 1:32 PM writes...

Hi. I appreciate the comments the given about the paper. As one of the authors of the paper (with Ramamoorthy on the NMR part), I would like to clear a few things as time permits.

@ Derek An uncharitable view would be that they have also taken aim at the year 1995, which is about when all three of these ideas were also being worked on for AD.

All three are still be working on and are in (mostly mixed or unsuccessful) clinical trials. Vitamin E in particular went through a phase III clinical trial for mild to moderate Alzheimer's with mixed results http://www.alzforum.org/news/research-news/trial-suggests-vitamin-e-protects-function-mild-alzheimers
To be fair, none of the other hypotheses have much support either.

@19 from Bob "The paper only uses the word drug once, in the context of including "drug-likeness" as a designed property, and therapeutics once in the conclusion."

Correct. I wasn't aware that at any point we claimed that this was a therapeutic or even a lead compound for a therapeutic. The discussion about drug discovery in academia vs. industry, while interesting, is in my opinion somewhat off-topic. A more relevant question is whether it is worth investigating one compound with a detailed approach (which you are going to have do if you want in any kind of mechanism based inhibitor) or try a high-throughput non-mechanistic approach phenotypic screening. I'm agonist on this point and i think both are viable (or a maybe both non-viable options). Large scale phenotypic screening for Alzheimer's is going to exceed the resources of academic lab. Based on the amount of money spent on pharma and the current success rate, I suspect its been tried on some level and failed at relatively early stage.

@21 from JSR "If the end result of months or years of work by 14 authors and almost as many sources of funding...

The non mass spec work (the bulk of the paper) was supported by a single R21 and a private foundation grant of which this paper is a small part.

@21 from JSR "not ready to publish, especially not in the once hallowed pages of JACS."
"MedChem journals likely would have asked that more work be done to answer some of the same questions Derek raised."
@35 "I’d add ‘who partners with someone who knows how to build / run relevant screening assays"

There are no relevant high-throughput screening assays for amyloid inhibition in common use. This point in particular I would like to stress and is the reason (as one of the commenters guessed) we left some of the expected the out of the paper. A very high percentage of the papers in JACS and J. Med. Chem on amyloid inhibitors consist of a set of compounds with only three sets of data. A high-throughput thioflavin T assay to measure amyloid inhibition, a set of EM images to show amyloid disappearing, and an MTT assay. There is very rarely any kind of pharmokinetics often not even to the extant of calculating drug-likedness (if you don't believe me look up amyloid inhibitor on basically any journal including the med chem ones). Though usually not acknowledged, ThT assay has a very high false positive rate since ThT generally binds at the same site as the inhibitor. Although not in the paper, we have shown this is true for the compound in the paper and many others. EM images suffer from multiple issues due to bias in binding to the grid, selection bias in sampling etc. The MTT assay has a sensitivity problem as suggested, and is not ideal for amyloid for a variety of other reasons.
The conformational antibodies sometimes used are also pretty non-specific, although this is only occasionally acknowledged in the literature. The end result is a lot of compounds with apparently quantifiable information that really isn't. There is no information on where the compound binds and what it binds to (amyloid beta is a mixture of many different, rapidly equilibrating species even when it is claimed to be in a single form).

If you have experience in high-throughput screening, I urge you to team up with an amyloid person (there are many amyloid specific factors that need to be considered). The field desperately needs you. Also, if you know of compounds for which reliable PK data has been obtained let me know (jbrender at umich.edu). I am compiling a database of amyloid inhibitors and an discouraged at what I am finding.

Our goal in the Ramamoorthy NMR lab in particular was to take a single compound and analyze its binding on low MW and fibrillar Abeta , using a labor intensive approach with the aim of developing a future high throughput fluorescence based approach to isolate specific interactions with different Abeta species (some unpublished progress has been made on the fluorescence work).
The study is only one of handful that have identified specific interactions in terms of a structure of Abeta (the new structure we have is the only high-resolution structure not in detergents in organic solvents). ML binds at a specific site on the structure, and looking back at the literature, you can see a similar binding site for many of the compounds in the literature. That to me at least is interesting.

In conclusion, it is not a complete story by any means, just a progress report. But a complete story with Abeta and Alzheimer's is going to take a very long time.

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44. JSR on January 10, 2014 4:53 PM writes...

Thanks to a couple of the authors for coming out and representing their work. I don't think anyone should, and I don't think anyone serious was trying to, disrespect the effort. There's no reason to bash academic or industrial research.

But I have limited time (not too limited, alas, to write this!). And with that limited time I peruse what I perceive to be the top journals in my areas. JACS is, or was, one of them. I don't think JACS is a good place for what is at most "just a progress report" (quoted from the author's post @43 above).

It's an idea, maybe a fanciful one, with a few interesting bits of data. Publish the progress in a thesis, publish the idea in a theoretical journal, or keep doing the hard work and publish the results in an appropriate journal.

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45. Quizzical on January 10, 2014 7:39 PM writes...

Eh, why isn't the journal publishing the article the one who gets to decide what is "appropriate" for their journal?

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46. WoW Chemist on January 10, 2014 10:28 PM writes...

Wow. So much anger. MTT issue? As you said, low cost. Ask the PI for compound and do it yourself. Just sign the "I won't commercialize" form. It's NIH funded and they have to make available for checks ect. Other issues? If you care do it. If you think the data are false say which. Compound is makable...Don't just dog a pony so you can get ahead. This is science. If you're so great do the experiment and show

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47. whoami on January 11, 2014 2:37 AM writes...

A ballpark estimate of the binding constant can be obtained from the NMR techniques used to identify the qualitative binding. If the chemical shift perturbation is weak in the peptide-ligand titration, then it is a weak binding case, with K_d in the range of ~1-100 mM. Along with perturbation, if line-broadening also occurs, K_d is in 1mM- 1uM range. If new sets of peaks appear in addition to the old/parent peaks, then the K_d is in 0.1uM-nM. Also if experiments like STD NMR works with positive results then the binding affinity falls within 100mM-1uM range. Though such details are not explicitly mentioned in the paper i think the readers can easily guess it by evaluating the limitation of the techniques used for this study.

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48. MoMo on January 11, 2014 6:55 PM writes...

Drug discovery and organic chemistry is not owned by academia or industry, but by those who devote their time, effort and valuable life force to the pursuit of compounds that may alleviate suffering.

So tell us all how innovation should be done-o ' great minds on both sides!

The smart will listen, the frustrated and lost will criticize.

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49. anon the II on January 12, 2014 8:57 AM writes...

@ MoMo

I don't think this is an academia vs. industry issue. This is about a lame-ass paper making it into JACS. We're all "frustrated and lost" when it comes to making drugs but we're smart enough to know that a one compound paper will not lead us anywhere useful and we're annoyed that a Journal that should separate useful from useless didn't do avery good job this time. So this "O Great Mind" is telling you that you should make more than one compound, especially when it's just a reductive amination. You can't draw a useful line through just one point. The frustration is that more "valuable life force" should have gone into this work prior to publication, especially in a formerly respected journal.

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50. Anonymous on January 12, 2014 2:22 PM writes...

As someone who has experience with abeta, I would like to thank #43 JR Brender for commenting on the issues with amyloid assays.

The problems with conformation and aggregation assays are definitely under-acknowledged in the literature. I really don't understand how much of the "high-impact" work gets published in this field.

"The conformational antibodies sometimes used are also pretty non-specific" True dat!

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51. Piero on January 13, 2014 4:17 AM writes...

Too bad this is turning into a fight industry vs academia, with such angry and offensive wording from both parts

I think Derek's thoughts were quite equilibrated (maybe a bit biased towards "industry usefulness"... I'm also in the industry, for the record) but many of the rest aren't

Academia don't have the power/money to go full throttle into drug discovery, so one should expect their publications would be more elucidation/starting points, and this is fine without the need for bashing them

The arguing then should go if this article succeeds in this or not, and if it is sound science (I'm not deciding not having read the article and probably not having sufficient
knowledge).. it certainly tries to.

A take-home message is that guys from industry don't consider this something that would be useful for them to proceed to drug discovery, and this is something that the authors should keep in mind should they would like to go this direction or find some partners for developing

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52. SAR Screener on January 13, 2014 6:22 AM writes...

43. JR Brender
I was comment 35. It wasn't meant to be a swipe at the paper / academic pharma research, more a grumble at the comments that seem to think that having an experienced med chemist on board will solve everything. It won't.

If you’d like to team up with assay dev groups, there are quite a few academic labs / consortia such as the MRCT and ELF (sorry, I only really know the European ones) that may be able to help / point you in the direction of someone else or there’s always pharma companies themselves.

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53. Chris on January 13, 2014 11:39 AM writes...

I am struggling with this one. I read with interest Derek's original post, then watched the mud start to fly. I feel like I must contribute here, but am not sure what to say.

As an academic chemist (in a medical school environment, not a basic science department) I am often appalled at how many of my colleagues in the basic sciences claim to be doing something applied (methodologies that will help in drug synthesis, novel compounds that will have therapeutic value, analytical techniques that will help with diagnosis) when what they are doing is unlikely to ever have any practical application. What they are really doing is science for the sake of science. But these days, you have to pretend that there is some direct application of your work or else you will never get funding and have significant difficulty publishing your work.

In the case of this work, I have heard the PI speak about the project a few times and have had the same "so what" response as many above. On the one hand, the work did its job: securing funding and a JACS paper that helped the lead PI get tenure. On the other hand, why not work on something that has a fighting chance of making a difference in the field while you're at it.

I think that the answer here is that it's VERY difficult to do that. Especially for a scientist who is well trained in one field but not so strong in others (such as a synthetic chemist who is weak on the biology, or vice versa). This is where I struggle in my own work. I REALLY want to do something that will make an impact, something that will leave the field better than I found it (I don't work in Alzheimer's, by the way, WAY too complicated for me). But it is a real struggle to do that. It's much easier to just push forward with incremental advances, keeping the lab funded and the papers flowing. I don't think industrial scientists can argue with this - my understanding is that few who work in industry will ever actually work on a drug that makes it to market.

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54. Mfernflower on January 13, 2014 5:58 PM writes...

It looks *okay* I mean it does not look like any block busting drug. Its too simple and could have too many reaction sites. Its not as bad as the nitrated DDT derivative that was posted about as being a agonist of a obscure as all monkey's receptor, GPR35. (also did I mention that it contains 4 nitro-groups. 2 hydroxide groups and a nasty DDT like dichloroalkene head!)
The quinoline core could use some work however.
A lot of work........

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55. z on January 13, 2014 6:46 PM writes...

In reading some of these comments, there's one stream of thought that I just can't follow: that academia should be able to get away with doing fewer things than industry because academia has fewer resources. Science is science no matter who is paying the bills. If you are working on a project that requires certain kinds of data, then you should make sure you have the resources to acquire that data, otherwise maybe you should be working on a different kind of project.

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