“Keeping sight of the bigger picture is essential”
The stated aim of medical research is to cure disease. And yet, when clinical trials prove unsuccessful, research labs and pharmaceutical companies alike too often fail to adjust their strategies. A conversation with neuroscientist and Nobel laureate Thomas Südhof on abysmal studies, effective research funding—and the Alzheimer’s debacle.
Thomas Südhof, have you ever climbed Mount Everest?
No. (laughs)
I could well imagine you have. In your research, you set your sights on the highest peaks: you study what is possibly the most complex organ in our body, the brain. What led you to do so?
The brain may well be our most complex organ. It makes us who we are, something that has always fascinated me. But we shouldn’t underestimate how many secrets other organs still hold. Even the cell, the smallest unit in an organism, whether animal or plant, is complex and not yet understood.
The more closely we look, the more complicated it gets.
Yes. Originally, I studied medicine. My desire to understand is what motivated me. After earning my doctorate, I began researching cholesterol transport because I wanted to gain deeper insight into how lipid metabolic disorders develop. Although I saw that much remained to be discovered in this area, I also realised that quite a bit was already known—and that outstanding scientists were hard at work on the problems. The brain was largely unexplored at the time, so there were great possibilities for researchers. That was what lay behind my decision to go into brain research.
You’re specialised in synapses, the junctions between neurons in the brain. What makes them important?
Synapses are nodes where neurons communicate. But they’re also the central processing units in our brains. When one neuron transmits information to another, the signal isn’t simply passed on: it changes at the synapse. And still, most neurobiologists focus on the neurons—counting how many times they fire—without considering the synapses. What’s truly significant, however, is how the information encapsulated in the firing of neurons is transmitted and, in the process, recalculated. This varies from synapse to synapse: there are many different kinds of synapse, with every neuron having thousands, tens of thousands and sometimes even hundreds of thousands of them.
It’s an incredibly complex system.
That’s why synapses are often overlooked in theories by systems neurobiologists, although they’re involved in everything the brain does. Conditions like neurodegeneration, epilepsy, autism, schizophrenia or Tourette’s syndrome are ultimately all linked to synapses. The problem is that we don’t understand most brain disorders, we don’t know what causes them. Alzheimer’s disease is a prime example.
With regard to Alzheimer’s in particular, many attempts have been made to cure it. But there have also been many setbacks. Are you surprised?
Not in the least. Roughly thirty years ago, it was discovered that a small peptide called amyloid beta is a major factor in Alzheimer’s disease; its exact role, however, is still unclear. What we do know is that this peptide is deposited in the form of insoluble accumulations—plaques—that are found in the brains of all patients with Alzheimer’s. These plaques are formed already ten, twenty, even thirty years before the first symptoms present. Among many researchers, the conviction that the peptide itself is toxic gained ground, so the pharmaceutical companies all began developing medications that alter the amyloid beta or its production, and millions upon millions were invested. That made sense, no question about it.
“Made” sense?
At first, yes. But after many, many clinical trials, it became clear that suppressing the enzymes responsible for amyloid beta exacerbates symptoms of Alzheimer’s. In short, the medications were making the disease worse. This result is actually unsurprising, especially if we think that these enzymes process a range of different substances, making them important for the brain’s functioning. Afterwards, there was a series of clinical trials that removed amyloid beta directly from the brain, but no substantial improvement in patient health was detected.
“Conditions like Alzheimer’s, epilepsy, autism and schizophrenia are ultimately all linked to synapses. The problem is that we don’t understand most brain disorders.”
There seems to be a lack of basic knowledge about how the brain functions. Were the clinical trials started too early because a drug to treat Alzheimer’s would be highly lucrative?
A very good question. The relationship between basic research and clinical studies is complex. Sometimes it’s necessary to begin clinical trials before we understand everything to the last detail. This is the case when the need for a treatment is extremely dire and a mechanism seems plausible. With amyloid beta, the original trials were justified. But the real question is: what happens when it becomes clear that an approach won’t result in significant progress? With amyloid beta, the original studies showed that it’s possible to remove the peptide from a patient’s brain—but without attaining a measurable improvement in patient health. That’s why it really no longer made sense to continue working in this direction in order to develop similar, maybe minimally better antibodies. It would make more sense to invest in basic research and gain a better understanding of the disease.
What problems arise when an unpromising approach is nevertheless continued?
Ethical, financial problems—and those that implicate research practice itself. Patients are subjected to experiments that will clearly never succeed, which is unethical. In addition, clinical trials cost pharmaceutical companies billions, money that could be invested in other trials at these companies. Patients, too, are unavailable for other studies. And university hospitals, which are frequently involved in these projects, are left with fewer resources for other work.
And so research stagnates?
Precisely. The wrong signals are sent. The pressure to conduct applied research is growing in numerous countries. When pharmaceutical companies invest billions in amyloid beta toxicity, governments believe it’s the way forward —and they, too, fund projects in the same area. That means wasted money, lost opportunities.
All this has consequences. Science currently has a credibility problem in society, and it’s partly because so many mistakes are being made.
Is it also because study findings are later proven to be incorrect?
Yes, certainly, it’s a huge problem. Science publishing is a broken business. We can no longer trust journals to honestly review articles, and pharmaceutical companies can no longer rely on published findings.
Not even research findings published in top-tier journals?
Exactly. Today, if a pharmaceutical company finds a study interesting, it repeats the investigation in-house, which is an absolute waste of money. But they do it because quality control is abysmal, even at the best journals.
Why?
Commercial reasons. The journals are interested in publishing as many papers as possible to make money.
Does this then impact research funding, which is awarded mainly on the basis of publications?
Of course. The publishing industry is currently the biggest problem in academic research. It’s even worse than the lack of money, worse than anything else, in fact.
How could we solve the problem?
Through regulation. Science publishing is the largest industry in the western world that isn’t regulated. Journals can publish what they want. They can make any assertion they please. There’s no liability, no accountability. There are companies that own hundreds, even thousands of journals. It’s like the Wild West.
So we have no way to know how good a journal is.
That’s right, and if they publish incorrect information, it’s never retracted.
If false data are published, aren’t researchers held accountable?
No. And while the system will correct itself eventually, it takes a long time. This mainly happens in that false findings never lead to anything viable. The studies are still accessible and are cited, but no therapies or real-world applications based on them are ever developed. Amyloid beta is a good example. Many, many studies on the peptide have been published in renowned journals, but most are wrong.
For example?
One study maintained it’s possible to diagnose Alzheimer’s by detecting amyloid beta in skin biopsies. Utter nonsense. Other researchers removed the ovaries of mice to simulate menopause. The study—published in Nature—claimed this led to a loss of up to fifty percent of all synapses and would explain why postmenopausal women develop Alzheimer’s more often. Can you really imagine that women generally lose half their synapses in the brain during menopause? It’s not very plausible. And then there’s the recent discovery that data in an influential Nature paper on amyloid beta published nearly twenty years ago were falsified. It all illustrates
how problematic the business of science publishing is.
“The publishing industry is currently the biggest problem in academic research. Worse even than the lack of money.”
Has this uncovering of bad practices had a positive impact on Alzheimer’s research?
I’m not certain, but I think so. In the meantime, it’s become clear that studying amyloid beta alone won’t get us anywhere. That’s why all the research now is focusing on another aspect: immune cells called microglia. Suddenly, most researchers are convinced that Alzheimer’s is linked to an immune reaction—certainly true, but it doesn’t explain everything. The same labs that published papers in Nature about amyloid beta are now publishing articles about microglia in Nature. Just like lemmings. (laughs)
Do you think the people and institutions sponsoring and funding research should make an effort to help improve the situation?
Yes, and that includes foundations like the Werner Siemens Foundation. The most important criterion for awarding funding should be quality. When evaluating proposals, it’s important for experts to not lose sight of the bigger picture, to keep track of an entire field—and not just focus on the latest findings and trends.
Do you see fundamental differences in how funding is awarded in the US and Europe?
Yes, I do. In the US, almost all research is financed through third parties. For example, Stanford University doesn’t pay my salary: the money stems from third-party funds at the Howard Hughes Medical Institute—and I have to reapply for my research funding every five years.
I noticed you even have a donate button on your group’s website. That’s rarely seen in Europe.
(Laughs) Unfortunately, it doesn’t work.
It doesn’t hurt to try.
In Europe, at least in Germany, all major labs are permanently funded—and they’re often huge. At Stanford, there are a few labs that are really big, but most—mine included—employ twenty-five researchers tops. A lot of my former postdocs in Europe have much larger labs. Although they, too, have to submit applications to third parties, these funds often make up less than half of the overall financing. Both systems have their advantages and disadvantages. The good thing in the US is that researchers are held accountable for their work at all times. As a result, the money is often awarded wisely.
And the disadvantage?
The pressure is huge. Fewer and fewer people are interested in pursuing a career in research. There’s no security, you constantly have to work at drumming up money for your salary and research. It’s especially difficult for women who want to have children. We need to do more there.
“The most important criterion for awarding funding should be quality. When evaluating proposals, keeping sight of the bigger picture is essential.”
In Europe, too, there’s no guarantee of a professorship after a postdoc.
But if you have a job in Europe, you have it for the long term. On the downside, however, this means that researchers might just keep doing the same thing. They’re no longer motivated to prove anything, they’re situated comfortably within a gigantic apparatus and don’t produce much that’s new. The other problem in Europe is that the research world is too small. In Germany, everyone knows everyone. Even more so in Austria and Switzerland. The result is that nepotism in research funding is on the rise.
You’ve made major advances in your field and have received numerous honours, including the Nobel Prize, the most prestigious of them all. What makes you such a good researcher?
(Laughs and thinks for a long time) I have a strong tendency towards independence and scepticism, which is both good and bad. It’s helpful in that these qualities make me resistant to trends and help me to critically question accepted opinions. Independent, critical thinking is of utmost importance in science. I believe it’s my strength. But it’s also a weakness. I don’t feel comfortable working in bureaucracies or larger teams. I’ve never been president of anything, as other qualities are needed for those kinds of roles.
What’s your advice for young researchers?
It’s important to know your own strengths and weaknesses. People who excel at devising specialised experiments should be the ones trying to solve scientific problems. But those with a talent for networking, teamwork and communication should work on interdisciplinary projects, or they should tackle issues that are of interest to governments. Both kinds of researchers should work and conduct research at universities. We need both.