Serotonin, depression, neurogenesis, and the beauty of science

If you asked any self-respecting neuroscientist 25 years ago what causes depression, she would likely have only briefly considered the question before responding that depression is caused by a monoamine deficiency. Specifically, she might have added, in many cases it seems to be caused by low levels of serotonin in the brain. The monoamine hypothesis that she would have been referring to was first formulated in the late 1960s, and at that time was centered primarily around norepinephrine. But in the decades following the birth of the monoamine hypothesis, its focus shifted to serotonin, in part due to the putative success of antidepressant drugs that targeted the serotonin transporter (e.g. selective serotonin reuptake inhibitors, or SSRIs). The monoamine/serotonin hypothesis eventually became generally recognized as viable by the scientific community. Interestingly, it also became widely accepted by the public, who were regularly exposed to television commercials for antidepressant drugs like Prozac, Lexapro, and Celexa--drugs whose commercials specifically mentioned a serotonin imbalance as playing a role in depression.

Over the years, however, the scientific method quietly and efficiently went to work. Evidence gradually accumulated that indicated that the serotonin hypothesis does a very inadequate job of explaining depression. For example, although SSRIs increase serotonin levels within hours after drug administration, if their administration leads to beneficial effects--a big if--it usually takes 2-4 weeks of daily administration for those effects to appear. One would assume that if serotonin levels were causally linked to depression, then soon after serotonin levels increased, mood would begin to improve. Also, reducing levels of serotonin in the brain does not cause depression. The list of studies that don't fully support the serotonin hypothesis of depression is actually quite lengthy, and most of the scientific community now agrees that the hypothesis is insufficient as a standalone explanation of depression.

In the 1990s another hypothesis, known as the neurogenic hypothesis, was proposed with the hopes of filling in some of the holes in the etiology of depression that the monoamine hypothesis seemed to be unable to fill. The neurogenic hypothesis suggests that depression is at least partially caused by an impairment of the brain's ability to produce new neurons, a process known as neurogenesis. Specifically, researchers have focused on neurogenesis in the hippocampus, one of the only areas in the brain where neurogenesis has been observed in adulthood (the other being the subventricular zone).

The neurogenic hypothesis was formulated based on several observations. First, depressed patients seem to have smaller hippocampi than the general population, and their hippocampi also appear to be smaller during periods of depression than during periods of remission. Second, glucocorticoids like cortisol are elevated in depression, and glucocorticoids appear to inhibit neurogenesis in the hippocampus in rodents and non-human primates. Finally, there is evidence that the chronic administration of antidepressants increases neurogenesis in the hippocampus in rodents.

The neurogenic hypothesis thus suggests that depression is associated with a reduction in the birth of new neurons in the hippocampus, an area of the brain important to stress regulation, cognition, and mood. According to this hypothesis, when someone takes antidepressants, the drugs do raise levels of monoamines like serotonin, but they also enact long-term processes that increase neurogenesis in the hippocampus. This neurogenesis is hypothesized to be a crucial part of the reason antidepressants work, and the fact that it takes some time for hippocampal neurogenesis to return to normal may help to explain why antidepressants take several weeks to have an effect.

This may all sound logical, but the neurogenic hypothesis has its own share of problems. For example, while stress-related impairment of neurogenesis has been observed in rodents, we don't have definitive evidence it occurs in humans. Human studies thus far have relied on comparing the size of the hippocampi in depressed and non-depressed patients. While smaller hippocampi have been observed in depressed individuals, it is not clear that this is due to reduced neurogenesis rather than some other type of structural changes that might have occurred during depression.

Similarly, while the administration of antidepressants has been associated with increased neurogenesis in rodent models of stress, we don't have clear evidence of this in humans. In humans we again have to rely on looking at things like hippocampal size. Because there could be a number of explanations for changes in the size of the hippocampi, we can't assume neurogenesis is the sole factor involved--or that it is involved at all. Additionally, some studies in rodents have found that antidepressants lead to a reduction in anxiety or depressive symptoms in the absence of increased hippocampal neurogenesis.

Another problem is that when neurogenesis is experimentally decreased in rodents, the animals don't usually display depressive symptoms. Experiments of this type haven't been performed with humans or non-human primates, so we don't know if a reduction in neurogenesis in any species is actually sufficient to cause depression. And no studies have found that increasing neurogenesis alone is enough to alleviate depressive-like symptoms.

Of course none of this means the neurogenic hypothesis is incorrect, but it does suggest there is a long way to go before we can feel confident about incorporating it fully into our understanding of depression. In the reluctance of the scientific community to embrace this hypothesis is where I see the beauty of science. Although it took decades of testing and revising before the monoamine hypothesis became a widely accepted explanation for depression, one could argue (based on its now recognized shortcomings) that we accepted it too readily.

However, it seems that many in the scientific community have learned from that mistake. Although there is no shortage of publications whose authors may be too willing to anoint the neurogenic hypothesis as a new unifying theory of depression, overall the tone when speaking of the neurogenic hypothesis seems to be cautious and/or critical. There is also a great deal of discussion now in the literature about the complexity of mood disorders like depression, and how it is unlikely to be able to explain their manifestation in a diverse population of individuals with just one mechanism, whether it be impaired neurogenesis or a serotonin deficiency.

Thus, the neurogenic hypothesis will require much more testing before we can consider it an important piece in the puzzle of depression. Even if further testing supports it, however, it will likely be considered just that--a piece in the puzzle, instead of an overarching explanation of the disorder. And that circumspect approach to explaining depression represents an important advancement in the way we look at psychiatric disorders.

See also: http://www.neuroscientificallychallenged.com/blog/2008/04/serotonin-hypothesis-and-neurogenesis

Miller, B., & Hen, R. (2015). The current state of the neurogenic theory of depression and anxiety Current Opinion in Neurobiology, 30, 51-58 DOI: 10.1016/j.conb.2014.08.012

Autism, SSRIs, and Epidemiology 101

I can understand the eagerness with which science writers jump on stories that deal with new findings about autism spectrum disorders (ASDs). After all, the mystery surrounding the rapid increase in ASD rates over the past 20 years has made any ASD-related study that may offer some clues inherently interesting. Because people are anxiously awaiting some explanation of this medical enigma, it seems like science writers almost have an obligation to discuss new findings concerning the causes of ASD.

The problem with many epidemiological studies involving ASD, however, is that we are still grasping at straws. There seem to be some environmental influences on ASD, but the nature of those influences is, at this point, very unclear. This lack of clarity means that the study of nearly any environmental risk factor starts out having potential legitimacy. And I don't mean that as a criticism of these studies--it's just where we're at in our understanding of the rise in ASD rates. After we account for mundane factors like increases in diagnosis due simply to greater awareness of the disorder, there's a lot left to figure out.

So, with all this in mind, it's understandable (at least in theory) to me why a study published last week in the journal Pediatrics became international news. The study looked at a sample of children that included healthy individuals along with those who had been diagnosed with ASD or another disorder involving delayed development. They asked the mothers of these children about their use of selective serotonin reuptake inhibitors (SSRIs) during pregnancy. 1 in 10 Americans is currently taking an antidepressant, and SSRIs are the most-frequently prescribed type of antidepressant. Thus, SSRIs are administered daily by a significant portion of the population.

Before I tell you what the results of the study were, let me tell you why we should be somewhat cautious in interpreting them. This study is what is known as a case-control study. In a case-control study, investigators identify a group of individuals with a disorder (the cases) and a group of individuals without the disorder (the controls). Then, the researchers employ some method (e.g. interviews, examination of medical records) to find out if the cases and controls were exposed to some potential risk factor in the past. They compare rates of exposure between the two groups and, if more cases than controls had exposure to the risk factor, it allows the researchers to make an argument for this factor as something that may increase the risk of developing the disease/disorder.

If you take any introductory epidemiology (i.e. the study of disease) course, however, you will learn that a case-control study is fraught with limitations. For, even if you find that a particular exposure is frequently associated with a particular disease, you still have no way of knowing if the exposure is causing the disease or if some other factor is really the culprit. For example, in a study done at the University of Pennsylvania in the late 1990s, researchers found that children who slept with nightlights on had a greater risk of nearsightedness when they got older. This case-control study garnered a lot of public attention as parents began to worry that they might be ruining their kids' eyesight by allowing them to use a nightlight. Subsequent studies, however, found that children inherit alleles for nearsightedness from their parents. Nearsighted parents were coincidentally more likely to use nightlights in their children's rooms (probably because it made it easier for the nearsighted parents to see).

A variable that isn't part of the researcher's hypothesis, but still influences a study's results is known as a confounding variable. In the case of the nearsightedness study, the confounding variable was genetics. Case-control studies are done after the fact, and thus experimenters have little control over other influences that may have affected the development of disease. Thus, there are often many confounding influences on relationships detected in case-control studies.

So, a case-control study can't be used to confirm a cause-and-effect connection between an exposure and a disorder or disease. What it can do is provide leads that scientists can then follow up on using a more rigorous experimental design (like a cohort study or randomized trial). Indeed, the scientific literature is replete with case-control studies that ended up being false leads. Sometimes, however, case-control results have been replicated with better designs, leading to important discoveries. This is exactly what happened with early reports examining smoking and lung cancer.

Back to the recent study conducted by Harrington et al. The authors found that SSRI use during the first trimester was more common in mothers whose children went on to develop ASD than in mothers who had children who developed normally. The result was only barely statistically significant. This fact combined with the variability seen in the confidence interval suggests it is not an overly-convincing finding--but it was a finding nonetheless. In addition to an increased risk of ASD, the authors also point out that SSRI exposure during the second and third trimesters was higher among mothers of boys with other developmental delays. Again, however, the effect was just barely statistically significant and even less convincing than the result concerning ASD.

So, the study ended up with some significant results that aren't all that impressive. Regardless, because this was a case-control design, there is little we can conclude from the study. To realize why, think about what other factors women who take SSRIs might have in common. Perhaps one of those influences, and not the SSRI use itself, is what led to an increased risk of ASD. For example, it seems plausible that the factors that make a mother more susceptible to a psychiatric disorder might also play a role in making her child more susceptible to a neurodevelopmental disorder. In fact, a cohort study published last year with a much larger sample size found that, when the influence of the condition women were taking SSRIs for was controlled for, there was no significant association between SSRI use during pregnancy and ASD.

The fact that this case-control study doesn't solve the mystery of ASD isn't a knock on the study itself. If anything, it's a knock on some of the science writing done in response to the study. I can't go so far as to say these types of studies shouldn't be reported on. But, they should be reported on responsibly, and by writers who fully understand and acknowledge their shortcomings. For, it is somewhat misleading to the general public (who likely isn't aware of the limitations of a case-control study) when headlines like this appear: "Study: Moms on antidepressants risk having autistic baby boys."

The safety of SSRI use during pregnancy is still very unclear. But both SSRIs and untreated depression during pregnancy have been linked to negative health outcomes for a child. Thus, using SSRIs during pregnancy is something a woman should discuss at length with her doctor to determine if treatment of the underlying condition poses more of a risk than leaving the condition untreated. In making that decision, however, the barely significant findings from a case-control study should not really be taken into consideration.

 

Rebecca A. Harrington, Li-Ching Lee, Rosa M. Crum, Andrew W. Zimmerman, Irva Hertz-Picciotto (2014). Prenatal SSRI Use and Offspring With Autism Spectrum Disorder or Developmental Delay PEDIATRICS DOI: 10.1542/peds.2013-3406d

Popular science writing and accuracy

This week, an article appeared in the L.A. Times online, and was recycled in the Chicago Tribune and a number of other media sources. It focused on a study that was just published in the Journal of Neuroscience. In the study, Iniguez et al. gave fluoxetine (aka Prozac) to male adolescent mice for 15 days. Three weeks after ending the fluoxetine treatment, the researchers tested the mice on two measures that are purported to assess depression in rodents and one that is a suggested measure of anxiety. They found that the mice previously treated with fluoxetine displayed less “depression-like” behavior, but more “anxiety-like” behavior.

The article in the L.A. Times was titled Prozac during adolescence protects against despair in adulthood. This title is problematic to me for a couple of reasons. First, because another species isn’t mentioned in the title, it is likely on first glance that most readers will assume that the finding occurred in, or was directly relatable to, humans. The author (Melissa Healy) mentions in the second paragraph that the study was done in mice, but continues to draw direct parallels to humans throughout the article. For example, Healy asks, “So how does a medication that treats depression in children and teens -- and that continues to protect them from depression as adults -- also heighten their sensitivity to stress?” when referring to the contradictory findings of increased anxiety and decreased depression-like behavior. The use of this vernacular (e.g. children and teens) makes it sound as if the observance made in the study means the same phenomenon would occur in humans who take Prozac. However, anyone who is familiar with rodent behavior knows that, for every behavior for which we can draw direct parallels to human behavior, there are many others for which the link is much more ambiguous.

Also, it is a bit of stretch to say that we can measure “despair” in mice. The researchers in this study used two tests to measure depression-like behavior: the response to social defeat stress and the forced-swim test. In the social defeat test, a mouse is forced to interact with another very aggressive mouse every day for 10 consecutive days. The aggressive mouse will typically force the experimental mouse into a subordinate position. After repeated exposure to this aggression, the subordinated mice become more submissive, antisocial, and withdrawn - symptoms which are thought to resemble human depression. These depression-like symptoms can be reversed with chronic antidepressant treatment. In the forced-swim test, mice are dropped into a beaker of water from which they cannot escape. Eventually, mice will stop trying to escape and move just enough to keep their head above water; this is interpreted as a form of helplessness, analogous to depression. Numerous experiments have shown, however, that acute treatment with antidepressants causes mice to continue attempting to escape for a longer period of time, which is taken as a sign of decreased depressive-like symptoms.

Do these tests measure depression in a way that is relevant to humans? Maybe, maybe not. There are those who would argue that we should be very cautious making such interpretations. Interestingly, one of the coauthors of the Iniguez et al. study, Eric J. Nestler (a prominent name in psychopharmacology research), wrote a paper in 2010 with Steven E. Hyman that focused on using animal models to understand human psychiatric disorders. The paper emphasized that many animal models are inadequate for making assumptions about human psychiatric conditions. Nestler and Hyman specifically mentioned the forced-swim test as one of two that “...are not models of depression at all. Instead, they are rapid, black-box tests developed decades ago to screen compounds for antidepressant activity.” They go on to say that the assumption that the increased activity in a forced swim test is related to alleviating depressive symptoms is an “...enormous anthropomorphic leap…” and that the test “...has not been convincingly related to pathophysiology.”

So, at least one coauthor in the Iniguez et al. study doesn’t seem to be completely confident that these types of findings are directly relatable to humans. Unfortunately, these doubts aren’t expressed within the Inguinez et al. paper. Instead, the authors use terms like “behavioral despair” when describing rodent behavior and fail to discuss limitations in attempting to relate their findings to a human population.

So, perhaps the author of the L.A. Times article isn’t completely to blame. I could argue that Iniguez et al. also could have been more specific about the implications of their study. However, I focused on the L.A. Times article because I feel like this sort of misinterpretation is rampant in popular science writing. Indeed, I have been guilty of it on this blog. It can often be well-intentioned. At least in my mind, the justification is that increasing interest in the article by the lay public increases interest in science in general, which is the goal of science writing - isn’t it?

Perhaps. It could be considered one goal of popular science writing, although one could argue that discussing science without taking a critical perspective is at odds with the historical tradition of science. Regardless, when speaking about a psychiatric disorder as common as depression, it may be a disservice to spread information that further supports the use of antidepressants. 11% of the American population already take antidepressants, and some studies have suggested that, except in the most severe cases, the difference between taking an antidepressant or placebo is small or negligible. For the superficial reader, the message of this L.A. Times article will clearly be that there are benefits to Prozac that go beyond simply treating depression at the point in time someone takes the drug. The message should, however, be that this study (if replicated) may tell us something about how rodents respond to antidepressants. What that means for humans, until a similar hypothesis is tested in humans, is completely unclear.


Iñiguez SD, Alcantara LF, Warren BL, Riggs LM, Parise EM, Vialou V, Wright KN, Dayrit G, Nieto SJ, Wilkinson MB, Lobo MK, Neve RL, Nestler EJ, Bolaños-Guzmán CA. (2014). Fluoxetine Exposure during Adolescence Alters Responses to Aversive Stimuli in Adulthood Journal of Neuroscience DOI: 10.1523/JNEUROSCI.5725-12.2014