Trusted source? The Conversation tells migraine sufferers that child abuse may be at the root of their problems

Patients and family members face a challenge obtaining credible, evidence-based information about health conditions from the web.

Migraine sufferers have a particularly acute need because their condition is often inadequately self-managed without access to best available treatment approaches. Demoralized by the failure of past efforts to get relief, some sufferers may give up consulting professionals and desperately seek solutions on Internet.

A lot of both naïve and exploitative quackery that awaits them.

Even well-educated patients cannot always distinguish the credible from the ridiculous.

One search strategy is to rely on websites that have proven themselves as trusted sources.

The Conversation has promoted itself as such a trusted source, but its brand is tarnished by recent nonsense we will review concerning the role of child abuse in migraines.

Despite some excellent material that has appeared in other articles in The Conversation, I’m issuing a reader’s advisory:

exclamation pointThe Conversation cannot be trusted because this article shamelessly misinforms migraine sufferers that child abuse could be at the root of their problems.

The Conversation article concludes with a non sequitur that shifts sufferers and their primary care physicians away from getting consultation with the medical specialists who are most able to improve management of a complex condition.

 

The Conversation article tells us:

Within a migraine clinic population, clinicians should pay special attention to those who have been subjected to maltreatment in childhood, as they are at increased risk of being victims of domestic abuse and intimate partner violence as adults.

That’s why clinicians should screen migraine patients, and particularly women, for current abuse.

This blog post identifies clickbait, manipulation, misapplied buzz terms, and  misinformation – in the The Conversation article.

Perhaps the larger message of this blog post is that persons with complex medical conditions and those who provide formal and informal care for them should not rely solely on what they find on the Internet. This exercise specifically focusing on The Conversation article serves to demonstrate this.

Hopefully, The Conversation will issue a correction, as they promise to do at the website when errors are found.

We are committed to responsible and ethical journalism, with a strict Editorial Charter and codes of conduct. Errors are corrected promptly.

The Conversation article –

Why emotional abuse in childhood may lead to migraines in adulthood

clickbaitA clickbait title offered a seductive  integration of a trending emotionally laden social issue – child abuse – with a serious medical condition – migraines – for which management is often not optimal. A widely circulating estimate is that 60% of migraine sufferers do not get appropriate medical attention in large part because they do not understand the treatment options available and may actually stop consulting physicians.

Some quick background about migraine from another, more credible source:

Migraines are different from other headaches. People who suffer migraines other debilitating symptoms.

  • visual disturbances (flashing lights, blind spots in the vision, zig zag patterns etc).
  • nausea and / or vomiting.
  • sensitivity to light (photophobia).
  • sensitivity to noise (phonophobia).
  • sensitivity to smells (osmophobia).
  • tingling / pins and needles / weakness / numbness in the limbs.

Persons with migraines differ greatly among themselves in terms of the frequency, intensity, and chronicity of their symptoms, as well as their triggers for attacks.

Migraine is triggered by an enormous variety of factors – not just cheese, chocolate and red wine! For most people there is not just one trigger but a combination of factors which individually can be tolerated. When these triggers occur altogether, a threshold is passed and a migraine is triggered. The best way to find your triggers is to keep a migraine diary. Download your free diary now!

Into The Conversation article: What is the link between emotional abuse and migraines?

Without immediately providing a clicklink so that  readers can check sources themselves, The Conversation authors say they are drawing on “previous research, including our own…” to declare there is indeed an association between past abuse and migraines.

Previous research, including our own, has found a link between experiencing migraine headaches in adulthood and experiencing emotional abuse in childhood. So how strong is the link? What is it about childhood emotional abuse that could lead to a physical problem, like migraines, in adulthood?

In invoking the horror of childhood emotional abuse, the authors imply that they are talking about something infrequent – outside the realm of most people’s experience.  If “childhood emotional abuse” is commonplace, how could  it be horrible and devastating?

In their pursuit of click bait sensationalism, the authors have only succeeded in trivializing a serious issue.

A minority of people endorsing items concerning past childhood emotional abuse actually currently meet criteria for a diagnosis of posttraumatic stress disorder. Their needs are not met by throwing them into a larger pool of people who do not meet these criteria and making recommendations based on evidence derived from the combined group.

Spiky_Puffer_Fish_Royalty_Free_Clipart_Picture_090530-025255-184042The Conversation authors employ a manipulative puffer fish strategy [1 and  2 ] They take what is a presumably infrequent condition and  attach horror to it. But they then wildly increase the presumed prevalence by switching to a definition that arises in a very different context:

Any act or series of acts of commission or omission by a parent or other caregiver that results in harm, potential for harm, or threat of harm to a child.

So we are now talking about ‘Any act or series of acts? ‘.. That results in ‘harm, potential for harm or threat’? The authors then assert that yes, whatever they are talking about is indeed that common. But the clicklink to support for this claim takes the reader behind a pay wall where a consumer can’t venture without access to a university library account.

Most readers are left with the authors’ assertion as an authority they can’t check. I have access to a med school library and I checked. The link is  to a secondary source. It is not a systematic review of the full range of available evidence. Instead, it is a  selective search for evidence favoring particular speculations. Disconfirming evidence is mostly ignored. Yet, this article actually contradicts other assertions of The Conversation authors. For instance, the paywalled article says that there is actually little evidence that cognitive behavior therapy is effective for people whose need for therapy is only because they  reported abuse in early childhood.

Even if you can’t check The Conversation authors’ claims, know that adults’ retrospective of childhood adversity are not particularly reliable or valid, especially studies relying on checklist responses of adults to broad categories, as this research does.

When we are dealing with claims that depend on adult retrospective reports of childhood adversity, we are dealing with a literature with seriously deficiencies. This literature grossly overinterprets common endorsement of particular childhood experiences as strong evidence of exposure to horrific conditions. This literature has a strong confirmation bias. Positive findings are highlighted. Negative findings do not get cited much. Serious limitations in methodology and inconsistency and findings generally ignored.

[This condemnation is worthy of a blog post or two itself. But ahead I will provide some documentation.]

The Conversation authors explain the discrepancy between estimates based on administrative data of one in eight children suffering abuse or neglect before age 18 versus much higher estimates from retrospective adult reports on the basis of so much abuse going unreported.

The discrepancy may be because so many cases of childhood abuse, particularly cases of emotional or psychological abuse, are unreported. This specific type of abuse may occur within a family over the course of years without recognition or detection.

This could certainly be true, but let’s see the evidence. A lack of reporting could also indicate a lack of many experiences reaching a threshold prompting reporting. I’m willing to be convinced otherwise, but let’s see the evidence.

The link between emotional abuse and migraines

The Conversation authors provide links only to their own research for their claim:

While all forms of childhood maltreatment have been shown to be linked to migraines, the strongest and most significant link is with emotional abuse. Two studies using nationally representative samples of older Americans (the mean ages were 50 and 56 years old, respectively) have found a link.

The first link is to an article that is paywalled except for its abstract. The abstract shows  the study does not involve a nationally representative sample of adults. The study compared patients with tension headaches to patients with migraines, without a no-headache control group. There is thus no opportunity to examine whether persons with migraines recall more emotional abuse than persons who do not suffer headaches.  Any significant associations in a huge sample disappeared after controlling for self-reported depression and anxiety.

My interpretation: There is nothing robust here. Results could be due to crude measurement, confounding of retrospective self-report by current self-report anxious or depressive symptoms. We can’t say much without a no-headache control group.

The second of the authors’ studies is also paywalled, but we can see from the abstract:

We used data from the Adverse Childhood Experiences (ACE) study, which included 17,337 adult members of the Kaiser Health Plan in San Diego, CA who were undergoing a comprehensive preventive medical evaluation. The study assessed 8 ACEs including abuse (emotional, physical, sexual), witnessing domestic violence, growing up with mentally ill, substance abusing, or criminal household members, and parental separation or divorce. Our measure of headaches came from the medical review of systems using the question: “Are you troubled by frequent headaches?” We used the number of ACEs (ACE score) as a measure of cumulative childhood stress and hypothesized a “dose–response” relationship of the ACE score to the prevalence and risk of frequent headaches.

Results — Each of the ACEs was associated with an increased prevalence and risk of frequent headaches. As the ACE score increased the prevalence and risk of frequent headaches increased in a “dose–response” fashion. The risk of frequent headaches increased more than 2-fold (odds ratio 2.1, 95% confidence interval 1.8-2.4) in persons with an ACE score ≥5, compared to persons with and ACE score of 0. The dose–response relationship of the ACE score to frequent headaches was seen for both men and women.

The Conversation authors misrepresent this study. It is about self-reported headaches, not the subgroup of these patients reporting migraines. But in the first of their own studies they just cited, the authors contrast tension headaches with migraine headaches, with no controls.

So the data did not allow examination of the association between adult retrospective reports of childhood emotional abuse and migraines. There is no mention of self-reported depression and anxiety, which wiped out any relationship with childhood adversity in headaches in the first study. I would expect that a survey of ACES would include such self-report. And the ACEs equate either parental divorce and separation (the same common situation likely occur together and so are counted twice) with sexual abuse in calculating an overall score.

The authors make a big deal of the “dose-response” they found. But this dose-response could just represent uncontrolled confounding  – the more ACEs indicates the more confounding, greater likelihood that respondents faced other social, person, economic, and neighborhood deprivations.  The higher the ACE score, the greater likelihood that other background characteristic s are coming into play.

The only other evidence the authors cite is again another one of their papers, available only as a conference abstract. But the abstract states:

Results: About 14.2% (n = 2,061) of the sample reported a migraine diagnosis. Childhood abuse was recalled by 60.5% (n =1,246) of the migraine sample and 49% (n = 6,088) of the non-migraine sample. Childhood abuse increased the chances of a migraine diagnosis by 55% (OR: 1.55; 95% CI 1.35 – 1.77). Of the three types of abuse, emotional abuse had a stronger effect on migraine (OR: 1.52; 95% CI 1.34 – 1.73) when compared to physical and sexual abuse. When controlled for depression and anxiety, the effect of childhood abuse on migraine (OR: 1.32; 95% CI 1.15 – 1.51) attenuated but remained significant. Similarly, the effect of emotional abuse on migraine decreased but remained significant (OR: 1.33; 95% CI 1.16 – 1.52), when controlled for depression and anxiety.

The rates of childhood abuse seem curiously high for both the migraine and non-migraine samples. If you dig a bit on the web for details of the National Longitudinal Study of Adolescent Health, you can find how crude the measurement is.  The broad question assessing emotional abuse covers the full range of normal to abnormal situations without distinguishing among them.

How often did a parent or other adult caregiver say things that really hurt your feelings or made you feel like you were not wanted or loved? How old were you the first time this happened? (Emotional abuse).

An odds ratio of 1.33 is not going to attract much attention from an epidemiologist, particularly when it is obtained from such messy data.

I conclude that the authors have made only a weak case for the following statement: While all forms of childhood maltreatment have been shown to be linked to migraines, the strongest and most significant link is with emotional abuse.

Oddly, if we jump ahead to the closing section of The Conversation article, the authors concede:

Childhood maltreatment probably contributes to only a small portion of the number of people with migraine.

But, as we will  see, they make recommendations that assume a strong link has been established.

Why would emotional abuse in childhood lead to migraines in adulthood?

This section throws out a number of trending buzz terms, strings them together in a way that should impress and intimidate consumers, rather than allow them independent evaluation of what is being said.

got everything

The section also comes below a stock blue picture of the brain.  In web searches, the picture  is associated with social media where the brain is superficially brought into  in discussions where neuroscience is  not relevant.

An Australian neuroscientist commented on Facebook:

Deborah on blowing brains

The section starts out:

The fact that the risk goes up in response to increased exposure is what indicates that abuse may cause biological changes that can lead to migraine later in life. While the exact mechanism between migraine and childhood maltreatment is not yet established, research has deepened our understanding of what might be going on in the body and brain.

We could lost in a quagmire trying to figuring out the evidence for the loose associations that are packed into a five paragraph section.  Instead,  I’ll make some observations that can be followed up by interested readers.

The authors acknowledge that no mechanism has been established linking migraines and child maltreatment. The link for this statement takes the reader to the authors own pay walled article that is explicitly labeled “Opinion Statement ”.

The authors ignore a huge literature that acknowledges great heterogeneity among sufferers of migraines, but points to some rather strong evidence for treatments based on particular mechanisms identified among carefully selected patients. For instance, a paper published in The New England Journal of Medicine with well over 1500 citations:

Goadsby PJ, Lipton RB, Ferrari MD. Migraine—current understanding and treatment. New England Journal of Medicine. 2002 Jan 24;346(4):257-70.

Speculations concerning the connections between childhood adversity, migraines and the HPA axis are loose. The Conversation authors their obviousness needs to be better document with evidence.

For instance, if we try to link “childhood adversity” to the HPA axis, we need to consider the lack of specificity of” childhood adversity’ as defined by retrospective endorsement of Adverse Childhood Experiences (ACEs). Suppose we rely on individual checklist items or cumulative scores based on number of endorsements. We can’t be sure that we are dealing with actual rather than assumed exposure to traumatic events or that there be any consistent correlates in current measures derived from the HPA axis.

Any non-biological factor defined so vaguely is not going to be a candidate for mapping into causal processes or biological measurements.

An excellent recent Mind the Brain article by my colleague blogger Shaili Jain interviews Dr. Rachel Yehuda, who had a key role in researching HPA axis in stress. Dr. Yehuda says endocrinologists would cringe at the kind of misrepresentations that are being made in The Conversation article.

A recent systematic review concludes the evidence for specific links between child treatment and inflammatory markers is of limited and poor quality.

Coelho R, Viola TW, Walss‐Bass C, Brietzke E, Grassi‐Oliveira R. Childhood maltreatment and inflammatory markers: a systematic review. Acta Psychiatrica Scandinavica. 2014 Mar 1;129(3):180-92.

The Conversation article misrepresents gross inconsistencies in the evidence of biological correlates representing biomarkers. There are as yet no biomarkers for migraines in the sense of a biological measurement that reliably distinguishes persons with migraines from other patient populations with whom they may be confused. See an excellent funny blog post by Hilda Bastian.

Notice the rhetorical trick in authors of The Conversation article’s assertion that

Migraine is considered to be a hereditary condition. But, except in a small minority of cases, the genes responsible have not been identified.

Genetic denialists like Oliver James  or Richard Bentall commonly phrased questions in this manner to be a matter of hereditary versus non-hereditary. But complex traits like height, intelligence, or migraines involve combinations of variations in a number of genes, not a single gene or even a few genes.. For an example of the kind of insights that sophisticated genetic studies of migraines are yielding see:

Yang Y, Ligthart L, Terwindt GM, Boomsma DI, Rodriguez-Acevedo AJ, Nyholt DR. Genetic epidemiology of migraine and depression. Cephalalgia. 2016 Mar 9:0333102416638520.

The Conversation article ends with some signature nonsense speculation about epigenetics:

However, stress early in life induces alterations in gene expression without altering the DNA sequence. These are called epigenetic changes, and they are long-lasting and may even be passed on to offspring.

Interested readers can find these claims demolished in Epigenetic Ain’t Magic by PZ Myers, a biologist who attempts to rescue an extremely important development concept from its misuse.

Or Carl Zimmer’s Growing Pains for Field of Epigenetics as Some Call for Overhaul.

What does this mean for doctors treating migraine patients?

The Conversation authors startle readers with an acknowledgment that contradicts what they have been saying earlier in their article:

Childhood maltreatment probably contributes to only a small portion of the number of people with migraine.

It is therefore puzzling when they next say:

But because research indicates that there is a strong link between the two, clinicians may want to bear that in mind when evaluating patients.

Cognitive behavior therapy is misrepresented as an established effective treatment for migraines. A recent systematic review and meta-analysis  had to combine migraines with other chronic headaches and order to get ten studies to consider.

The conclusion of this meta-analysis:

Methodology inadequacies in the evidence base make it difficult to draw any meaningful conclusions or to make any recommendations.

The Conversation article notes that the FDA has approved anti-epileptic drugs such as valproate and topiramate for treatment of migraines. However, the article’s claim that the efficacy of these drugs are due to their effects on epigenetics is quite inconsistent with what is said in the larger literature.

Clinicians specializing and treating fibromyalgia or irritable bowel syndrome would be troubled by the authors’ lumping these conditions with migraines and suggesting that a psychiatric consultation is the most appropriate referral for patients who are having difficulty achieving satisfactory management.

See for instance the links contained in my blog post, No, irritable bowel syndrome is not all in your head.

The Conversation article closes with:

Within a migraine clinic population, clinicians should pay special attention to those who have been subjected to maltreatment in childhood, as they are at increased risk of being victims of domestic abuse and intimate partner violence as adults.

That’s why clinicians should screen migraine patients, and particularly women, for current abuse.

It’s difficult to how this recommendation is relevant to what has preceded it. Routine screening is not evidence-based.

The authors should know that the World Health Organization formerly recommended screening primary care women for intimate abuse but withdrew the recommendation because of a lack of evidence that it improved outcomes for women facing abuse and a lack of evidence that no harm was being done.

I am sharing this blog post with the authors of The Conversation article. I am requesting a correction from The Conversation. Let’s see what they have to say.

Meanwhile, patients seeking health information are advised to avoid The Conversation.

Biomarker Porn: From Bad Science to Press Release to Praise by NIMH Director

Concluding installment of NIMH biomarker porn: Depression, daughters, and telomeres

Pioneer HPA-axis researcher Bernard “Barney” Carroll’s comment left no doubt about what he thought of the Molecular Psychiatry article I discussed in my last issue of Mind the Brain:

Where is the HPA axis dysregulation? It is mainly in the minds0@PubSubMain@NIHMS2@s@0@44595.html of the authors, in service of their desired narrative. Were basal cortisol levels increased? No. Were peak cortisol levels increased? They didn’t say. Was the cortisol increment increased? Only if we accept a p value of 0.042 with no correction for multiple comparisons. Most importantly, was the termination of the stress cortisol response impaired? No, it wasn’t (Table 3). That variable is a feature of allostasis, about which co-author Wolkowitz is well informed. Termination of the stress response is a crucial component of HPA axis regulation (see PubMed #18282566), and it was no different between the two groups. So, where’s the beef? The weakness of this report tells us not only about the authors’ standards but also about the level of editorial tradecraft on display in Molecular Psychiatry. [Hyperlink added]

You also can see my response to Professor Carroll in the comments.

I transferred  another  comment  to the blog from my Facebook wall. It gave me an opportunity to elaborate on why

we shouldn’t depend on small convenience samples to attempt to understand phenomena that must be examined in larger samples followed prospectively.

I explained

There are lots of unanswered questions about the authors’ sampling of adolescents. We don’t know what they are like when their mothers are not depressed. The young girls could also simply be reacting to environmental conditions contributing to their mother’s depression, not to their mother’s depression per se. We don’t know how representative this convenience sample is of other daughters of depressed mothers. Is it unusual or common that daughters of this age are not depressed concurrent with their mothers’ depression? What factors about the daughters, the mothers, or their circumstances determine that the mother and daughter depression does not occur at the same time? What about differences with him him dthe daughters of mothers who are prone to depression, but are not currently depressed?  We need to keep in mind that most biomarkers associated with depression are state dependent, not trait dependent. And these daughters were chosen because they are not depressed…

But with no differences in cortisol response, what are we explaining anyway?

The Molecular Psychiatry article provides an excellent opportunity to learn to spot bad

From  http://www.compoundchem.com/2014/04/02/a-rough-guide-to-spotting-bad-science/
From http://www.compoundchem.com/2014/04/02/a-rough-guide-to-spotting-bad-science/

science. I encourage interested readers to map what is said in that into the chart at the right.

This second installment of my two-part blog examines how the exaggerations and distortions of the article reverberate through a press release and then coverage in NIMH Director Thomas Insel’s personal blog.

The Stanford University press release headline is worthy of the trashy newspapers we find at supermarket checkouts:

Girls under stress age more rapidly, new Stanford study reveals

The press release says things that didn’t appear in the article, but echoes the distorted literature review of the article’s introduction in claiming well-established links between shortened telomeres, frequent infections in chronic disease and death that just are not there.

The girls also had telomeres that were shorter by the equivalent of six years in adults. Telomeres are caps on the ends of chromosomes. Every time a cell divides the telomeres get a little shorter. Telomere length is like a biological clock corresponding to age. Telomeres also shorten as a result of exposure to stress. Scientists have uncovered links in adults between shorter telomeres and premature death, more frequent infections and chronic diseases.

From http://news.stanford.edu/news/2014/october/telomeres-depression-girls-10-28-2014.html
From http://news.stanford.edu/news/2014/october/telomeres-depression-girls-10-28-2014.html

And the claim of “the equivalent of six years” comes from direct quote from obtained from senior author Professor Ian Gotlib.

“It’s the equivalent in adults of six years of biological aging,” Gotlib said, but “it’s not at all clear that that makes them 18, because no one has done this measurement in children.”

Dr. Gotlib  seems confused himself about what he mean by the 10 to 14-year-old girls having aged an additional six years. Does he really think that they are now 18? If so in what way? What could he possibly mean – do they look six years older than age matched controls? That would be really strange if they did.

I hope he lets us know when he figures out what he were saying, but he shouldn’t have given the statement to the Stanford press officer unless he was clear what he meant.

The press release noted that Dr. Gotlib had already moved on to intervention studies designed to prevent telomere shortening these girls.

In other studies, Gotlib and his team are examining the effectiveness of stress reduction techniques for girls. Neurofeedback and attention bias training (redirecting attention toward the positive) seem promising. Other investigators are studying techniques based on mindfulness training.

That’s a move based on speculation, if not outright science-fiction. Neurofeedback has some very preliminary evidence for effectiveness in treating current depression, but I would like to see evidence that it has any benefit for preventing depression in young persons who have never been depressed

neurofeedbackGotlib’s claims play right into popular fantasies about rigging people up with some sort of apparatus that changes their brain. But everything changes the brain, even reading this blog post. I don’t think that reading this blog post has any less evidence for preventing later depression than neurofeedback. Nonetheless, I’m hoping  that my blogging implants a healthy dose of skepticism in readers’ brains so that they are immunized against further confusion from exposure to such press releases. For an intelligent, consumer oriented discussion of neurofeedback, see Christian Jarrett’s

Read this before paying $100s for neurofeedback therapy

Attention bias training is a curious choice. It is almost as trendy as neurofeedback, but would it work?  We have the benefit of a systematic review and recent meta-analysis that suggests a lack of evidence for attention bias training in  treating depression and no evidence for preventing it. If it’s ineffectual in treating depression, how could we possibly expect it to prevent depression? Evidence please!

Let’s speculate about the implications if the authors found the cortisol differences between the daughters of the depressed mothers and daughters of controls that they had hypothesized but did not find. What then could have been done for these young girls? Note that the daughters of depressed mothers were chosen because they were functioning well, not currently depressed themselves. Just because they were different from the control girls would not necessarily indicate that any cortisol variables were in the abnormal range. Cortisol levels are not like blood pressure – we cannot specify a level below which cortisol levels have to be brought down for better health and functioning.

Note also that these daughters were selected on the basis of their mothers being depressed and that could mean the daughters themselves were facing a difficult situation. We can’t make the mother-bashing assumption that their mother’s depression was inflicting stress on them. Maybe any psychobiological stress response that was evident was due to the circumstances that led to the depression of their mother. We don’t know enough to specify what levels of cortisol variables would be optimal and consistent with good coping with the situation – we let even specify what is normal. And we don’t know how the daughters would recover from any abnormalities without formal treatment when their circumstances changed.

Bottom line is that these investigators did not get the results they hypothesized. Even if they had, results would not necessarily to lead to clinical applications.

Nonetheless, the director of NIMH saw fit to single this paper out or maybe he was just picking up on the press release.

my blogThomas Insel’s Personal Blog: Depression, Daughters, and Telomeres.

Thomas Insel’s Director’s Blog starts by acknowledging that there are no genetic or imaging markers predicting risk for depression, but research by Stanford Psychology Professor Ian Gotlib and colleagues in Molecular Psychiatry is “worth watching.”

Insel describes Gotlib’s “longitudinal” research as following depressed mothers’ early adolescent daughters.

The young girls have not yet developed depression, but 60 percent will become depressed by the age of 18.

I can find no basis in the article for Insel’s claim that Gotlib has found 60 per cent of these girls will be depressed by age 18. The estimate seems exaggerated, particularly given the case mix of mothers of these girls. It appears that some or most of the mothers were drawn from the community. We cannot expect severe course and biological correlates of depression that we would expect from a more inpatient sample.

Searching the papers coming out of this lab, I could only find one study involving a 30 month follow-up of 22 daughters of depressed mothers in the same age range as the sample in the Molecular Psychiatry article. That’s hardly a basis for the strong claim of 60% becoming depressed by 18.

Insel embellishes the importance of differences in telomere length. He perpetuates the illusion that we can be confident that differences in telomere length suggest these girls were experiencing accelerated aging and what have high risk for disease when the girls reached middle and late age. Without the backing of data from the paper or the existing literature, Insel zeros in on

Troubling early sign of risk for premature biological aging and possibly age-related chronic diseases, such as cardiovascular disease. Investigating the cause and timing of decreased telomere length—to what extent it may result from abnormalities in stress responses or is genetically influenced, for example—will be important for understanding the relationship between cellular aging, depression, and other medical conditions.

Insel ponders how such young, healthy girls could possibly show signs of aging. According to him the answer is not clear, but it might be tied to the increased stress reactivity these girls show in performing laboratory tasks.

But as Professor Caroll noted, the study just does not much evidence of “increased stress reactivity.”

neurofeedback2jpgNonetheless, Insel indicates that Gotlib’s next step is

Using neurofeedback to help these girls retrain their brain circuits and hopefully their stress responses. It will be a few years before we will know how much this intervention reduces risk for depression, but anything that prevents or slows the telomere shortening may be an early indication of success.

It’s interesting that Insel sidestepped the claim in the press release that Gotlib was trying out a cognitive behavioral intervention to affect stress reactivity. Instead he presents a fanciful notion that neural feedback will somehow retrain these girls’ brain circuits and reduce their stress response throughout their time at home and prevent them getting depressed by their mother’s depression.

Oh, if that were only so: Insel would be vindicated in his requiring for funding that researchers get down to basic mechanisms and simply bypass existing diagnoses with limited reliability, but at least some ties to patients’ verbal reports of why they are seeking treatment. In his world of science fiction, patients, or at least these young girls, which come in to have their brains retrained to forestall the telomere shortening that is threatening them not only with becoming depressed later, but with chronic diseases and middle and late life and early death.

So, let’s retrace what was said in the original Molecular Psychiatry article to what was claimed in the Stanford University press release and what was disseminated in the social media of Dr. Insel’s personal blog. Authors’ spin bad science in a peer-reviewed article. They collaborate with their university’s press relations department by providing even more exaggerated claims. And Dr. Insel’s purpose is served by simply passing them on and social media.

There’s a lot in Dr. Insel’s Personal Blog to disappoint and even outrage

  • Researchers  seeking guidance for funding priorites.
  • Clinicians in the trenches needing to do something now to deal with the symptoms and simple misery that are being presented to them.
  • Consumers looking for guidance from the Director of NIMH as to whether they should be concerned about their daughters and what they should do about it.

A lot of bad science and science fiction is being served to back up false promises about anything likely to occur in our lifetimes, if ever.

promising treatmentTaxpayers need to appreciate where Dr. Insel is taking funding of mental health with research. He will no longer fund grants that will explore different psychotherapeutic strategies for common mental health problems as they are currently understood – you know, diagnoses tied to what patients complain about. Instead he is offering a futuristic vision in which we no longer have to pay for primary care physicians or mental health clinicians spending time talking to patients about the problems in their lives. Rather, patients can bring in a saliva sample to assess the telomere length. They then can be rigged up to a videogame providing a social stress challenge. They will then be given neurofeedback and asked to provide another saliva sample. If the cortisol levels aren’t where they are supposed to be, they will come back and get some more neurofeedback and videogames.

But wait! We don’t even need to wait until people develop problems in their lives. We can start collecting spit samples when they are preteens and head off any problems developing in their life with neural feedback.

Presumably all this could be done by technicians who don’t need to be taught communication skills. And if the technicians are having problems, we can collect spit samples from them and maybe give them some neurofeedback.

Sure, mild to moderate depression in the community is a large and mixed grouping. The diagnostic category major depression loses some of its already limited reliability and validity when applied to this level of severity. But I still have a lot more confidence in this diagnosis than relying on some unproven notions about treating telomere length and cortisol parameters in people who do not currently complain about mental health or their circumstances. And the lamer notion that this can be done without any empathy or understanding.

It’s instructive to compare what Insel says in this blog post to what he recently said in another post.

He acknowledged some of the serious barriers to the development of valid, clinically useful biomarkers:

Patients with mental disorders show many biological abnormalities which distinguish them from normal volunteers; however, few of these have led to tests with clinical utility. Several reasons contribute to this delay: lack of a biological ‘gold standard’ definition of psychiatric illnesses; a profusion of statistically significant, but minimally differentiating, biological findings;‘approximate replications’ of these findings in a way that neither confirms nor refutes them; and a focus on comparing prototypical patients to healthy controls which generates differentiations with limited clinical applicability. Overcoming these hurdles will require a new approach. Rather than seek biomedical tests that can ‘diagnose’ DSM-defined disorders, the field should focus on identifying biologically homogenous subtypes that cut across phenotypic diagnosis—thereby sidestepping the issue of a gold standard.

All but the last sentence could have been part of a negative review of the Molecular Psychiatry article or the grant that provided funding for it. But the last sentence is the kind of nonsense that a director of NIMH can lay on the and research community and expect it to be reflected in their grant applications.

But just what was the theme of this other blog post from Dr. Insel? P-hacking and the crisis concerning results of biomedical research not being consistently reproducible.

The relentless quest for a significant “P” value is only one of the many problems with data analysis that could contribute to the reproducibility problem. Many mistakenly believe that “P” values convey information about the size of the difference between two groups. P values are actually only a way of estimating the likelihood that the difference you observe could have occurred by chance. In science, “significance” usually means a P value of less than 0.05 or 1 in 20, but this does not mean that the difference observed between two groups is functionally important. Perhaps the biggest problem is the tendency for scientists to report data that have been heavily processed rather than showing or explaining the details. This suggests one of the solutions for P-hacking and other problems in data analysis: provide the details, including what comparisons were planned prior to running the experiment.

Maybe because Insel is Director of NIMH, he doesn’t expect anybody to call him on the contradictions in what he is requesting. In the p-hacking blog post, he endorsed a call to action to address the problem of a lot of federal money being wasted on research that can’t lead to improvements in the health and well-being of the population because the research is simply unreliable and depends on “heavily processed” data for which investigators don’t provide the details. Yet in the Depression, Daughters, and Telomeres post he grabs an outrageous example of this being done and tells the research community he wants to see more of it.

 

porn

NIMH Biomarker Porn: Depression, Daughters, and Telomeres Part 1

Does having to cope with their mother’s depression REALLY inflict irreversible damage on daughters’ psychobiology and shorten their lives?

telomerejpg
Telomere

A recent BMJ article revived discussion of responsibility for hyped and distorted coverage of scientific work in the media. The usual suspects, self-promoting researchers, are passed over and their University press releases are implicated instead.

But university press releases are not distributed without authors’ approval.  Exaggerated statements in press releases are often direct quotes from authors. And don’t forget the churnaling journalists and bloggers who uncritically pass on press releases without getting second opinions.  Gary Schwitzer remarked:

Don’t let news-release-copying journalists off the hook so easily. It’s journalism, not stenography.

In this two-part blog post, I’ll document this process of amplification of the distortion of science from article to press release to subsequent coverage. In the first installment, I’ll provide a walkthrough commentary and critique of a flawed small study of telomere length among daughters of depressed women published in the prestigious Nature Publishing Group journal, Molecular Psychiatry. In the second, I will compare the article and press release to media coverage, specifically the personal blog of NIMH Director Thomas Insel.

whackI warn the squeamish that I will whack some bad science and outrageous assumptions with demands for evidence and pelt the study, its press release, and Insel’s interpretation with contradictory evidence.

I’m devoting a two-part blog to this effort. Bad science with misogynist, mother bashing assumptions is being touted by the  Director of NIMH as an example to be followed. When he speaks, others pay attention because he sets funding priorities. Okay, Dr. Insel, we will listen up, but we will do so skeptically.

A paper that shares an author with the Molecular Psychiatry paper was criticized by Daniel Engber for delivering

A mishmash of suspect stats and overbroad conclusions, marshaled to advance a theory that’s both unsupported by the data and somewhat at odds with existing research in the field.

The criticism applies to this paper as well.

But first, we need to understand some things about telomere length…

What is a Telomere?

Telomeres are caps on the ends of every chromosome. They protect the chromosome from losing important genes or sticking to other chromosomes. They become shorter every time the cell divides.

I have assembled some resources in an issue of Science-Based Medicine:

Skeptic’s Guide to Debunking Claims about Telomeres in the Scientific and Pseudoscientific Literature

As I say in that blog, there are many exaggerated and outright pseudoscientific claims about telomere length as a measure of “cellular aging” and therefore how long we’re going to live.

I explain the concepts of biomarker and surrogate endpoint, which are needed to understand the current fuss about telomeres. I show why the evidence is against routinely accepting telomere length as a biomarker or surrogate endpoint for accelerated aging and other health outcomes.

I note

  • A recent article in American Journal of Public Health claimed that drinking 20soda kills ounces of carbonated (but not noncarbonated) sugar-sweetened drinks was associated with shortened telomere length “equivalent to an approximately 4.6 additional years of aging.” So, effects of drinking soda on life expectancy is equivalent to what we know about smoking’s effect.
  • Rubbish. Just ignore the telomere length data and directly compare the effects of drinking 20 ounces soda to the effects of smoking on life expectancy. There is no equivalence. The authors confused differences in what they thought was a biomarker with differences in health outcomes and relied on some dubious statistics. The American Journal of Public Health soda study was appropriately skewered in a wonderful Slate article, which I strongly recommend.
  • Claims are made for telomere length as a marker for effects of chronic stress and risk of chronic disease. Telomere length has a large genetic component and is correlated with age. When appropriate controls are introduced, correlation among telomere length, stress, and health outcomes tend to disappear or get sharply reduced.
  • A 30-year birth cohort study did not find an association between exposure to stress and telomere length.
  • Articles from a small group of investigators claim findings about telomere lengths that do not typically get reproduced in larger, more transparently reported studies by independent groups. This group of investigators tends to have or have had conflicts of interest in marketing of telomere diagnostic services, as well as promotion of herbal products to slow or reverse the shortening of telomere length.
  • Generally speaking, reproducible findings concerning telomere length require large samples with well-defined phenotypes, i.e., individuals having well-defined clinical presentations of particular characteristics, and we can expect associations to be small.

Based on what I have learned about the literature concerning telomere length, I would suggest

  • Beware of small studies claiming strong associations between telomere length and characteristics other than age, race, and gender.
  • Beware of studies claiming differences in telomere length arising in cross-sectional research or in the short term if they are not reproduced in longitudinal, prospective studies.

A walk-through commentary and critique of the actual article

Gotlib, I. H., LeMoult, J., Colich, N. L., Foland-Ross, L. C., Hallmayer, J., Joormann, J., … & Wolkowitz, O. M. (2014). Telomere length and cortisol reactivity in children of depressed mothers. Molecular Psychiatry.

Molecular Psychiatry is a pay-walled journal, but a downloadable version of the article is available here.

Conflict of Interest Statement

The authors report no conflict of interest. However, in the soda article published December 2014, one of the authors of the present paper, Jun Lin disclosed being a shareholder in Telomere Diagnostics, Inc., a telomere measurement company. Links at my previous blog post take you to “Telomeres and Your Health: Get the Facts” at the website of that company. You find claims that herbal products based on traditional Chinese medicine can reduce the shortening of telomeres.

Jun Lin has a record of outrageous claims. For instance, in another article, that normal women whose minds wander may be losing four years of life, based on the association between self-reported mind wandering and telomere length. So, if we pit this claim against what is known about the effects of smoking on life expectancy, women can extend their lives almost as much by better paying attention as from quitting smoking.

Hmm, I don’t know if we have undeclared conflict of interest here, but we certainly have a credibility problem.

The Abstract

Past research shows distorted and exaggerated media portrayals of studies are often already evident in abstracts of journal articles. Authors engage in a lot of cherry picking and spin results to strengthen the case their work is innovative and significant.

The opening sentence of the abstract to this article is a mashup of wild claims about telomere length in depression and risk for physical illnesses. But I will leave commenting until we reach the introduction, where the identical statement appears with elaboration and a single reference to one of the author’s work.

The abstract goes on to state

Both MDD and telomere length have been associated independently with high levels of stress, implicating dysregulation of the hypothalamic-pituitary-adrenal (HPA) axis and anomalous levels of cortisol secretion in this relation.

hpa useWhen I showed this to a pioneer in the study of the HPA axis, he remarked:

If you can find coherence in this from the Abstract you are smarter than I am…The phrase dysregulation of the HPA axis has been used to support more hand waving than substance.

The abstract ends with

This study is the first to demonstrate that children at familial risk of developing MDD are characterized by accelerated biological aging, operationalized as shortened telomere length, before they had experienced an onset of depression; this may predispose them to develop not only MDD but also other age-related medical illnesses. It is critical, therefore, that we attempt to identify and distinguish genetic and environmental mechanisms that contribute to telomere shortening.

This breathless editorializing about the urgency of pursuing this line of research is not tied to the actual methods and results of the study. “Accelerated biological aging” and “predispose to develop… other age-related medical illnesses” is not a summary of the findings of the study, but only dubious assumptions.

Actually, the evidence for telomere length as a biomarker for aging is equivocal and does not meet American Federation of Aging Research criteria.  A large scale prospective study did not find that telomere length predicted onset of diabetes or cardiovascular disease.

And wait to when we examine whether the study had reproducible results concerning either shorter telomeres and depression or telomeres being related to cortisol reactivity.

The introduction

The 6-paragraph introduction packs in a lot of questionable assumptions backed by a highly selective citation of the literature.

A growing body of research demonstrates that individuals diagnosed with major depressive disorder (MDD) are characterized by shortened telomere length, which has been posited to underlie the association between depression and increased rates of medical illness, including cardiovascular disease, diabetes, metabolic syndrome, osteoporosis and dementia (see Wolkowitz et al.1 for a review).

Really? A study co-authored by Wolkowitz and cited later in the introduction actually concluded

telomere shortening does not antedate depression and is not an intrinsic feature. Rather, telomere shortening may progress in proportion to lifetime depression exposure.

“Exposure” = personal experience being depressed. This would seem to undercut the rationale for examining telomere shortening in young girls who have not yet become depressed.

But more importantly, nether the Molecular Psychiatry article nor the Wolkowitz review acknowledge the weakness of evidence for

  • Depression being characterized by shortened telomere length.
  • The association of depression and medical illness in older persons representing a causal role for depression that can be modified by or prevention or treatment of depression in young people.
  • Telomere length observed in the young underlying any association between depression and medical illnesses when they get old.

Wolkowitz’s “review” is a narrative, nonsystematic review. The article assumes at the outset that depression represents “accelerated aging” and offers a highly selective consideration of the available literature.

In neither it nor the Molecular Psychiatry article we told

  • Some large scale studies with well-defined phenotypes fail to find associations between telomeres and depressive disorder or depressive symptoms. One large-scale study co-authored by Wolkowitz found weak associations between depression and telomere length too small to be detected in the present small sample. Any apparent association may well spurious.
  • The American Heart Association does not consider depression as a (causal) risk factor for cardiovascular disease, but as a risk marker because of a lack of the evidence needed to meet formal criteria for causality. Depression after a heart attack predicts another heart attack. However, our JAMA systematic review revealed a lack of evidence that screening cardiac patients for depression and offering treatment reduces their likelihood of having another heart attack or improves their survival. An updated review confirmed our conclusions.
  • The association between recent depressive symptoms and subsequent dementia is evident with very low level of symptoms, suggesting that it reflects residual confounding and reverse causation  of depressive symptoms with other risk factors, including poor health and functioning. I published a commentary in British Medical Journal  that criticized  claim that we should begin intervening for even low symptoms of depression in order to prevent dementia. I suggested that we would be treating a confound and it would be unlikely to make a difference in outcomes.

I could go on. Depression causally linked to diabetes via differences in telomere length? Causing osteoarthritis? You gotta be kidding. I demand quality evidence. The burden of evidence is on anyone who makes such wild claims.

Sure, there is lots of evidence that if people have been depressed in the past, they are more likely to get depressed again when they have a chronic illness. And their episodes of depression will last longer.

In general, there are associations between depression and onset and outcome of chronic illness. But the simple, unadjusted association is typically seen at low levels of symptoms, increases with age and accumulation of other risk factors and other physical co-morbidities. People who are older, already showing signs of illness, or who have poor health-related behaviors tend to get sicker and die. Statistical control for these factors reduces or eliminates the apparent association of depressive symptoms with illness outcomes. So, we are probably not dealing with depression per se.  If you are interested in further discussion of this see my slide presentation, see

Negative emotion and health: why do we keep stalking bears, when we only find scat in the woods?

I explain risk factors (like bears) versus risk markers (like scat) and why shooting scat does not eliminate the health risk posed by bears,.

I doubt few people familiar with the literature believe that associations among telomeres and depression, depression and the onset of chronic illness, and telomeres and chronic illness are such that a case could be made for telomere length in young girls being importantly related to physical disease in their mid and late life. This is science fiction being falsely presented as evidence-based.

The authors of the Molecular Psychiatry paper are similarly unreliable when discussing “dysregulation of the hypothalamic-pituitary-adrenal (HPA) axis and anomalous levels of cortisol secretion.” You would think that they are referring to established biomarkers for risk of depression. Actually, most biological correlates of depression are modest, nonspecific to depression, and state, not trait-related – limited to when people are actually depressed.

MDD and ND [nondepressed] individuals exhibited similar baseline and stress cortisol levels, but MDD patients had much higher cortisol levels during the recovery period than their ND counterparts.

We did not find the expected main effects of maternal depression on children’s cortisol  reactivity.

  • They misrepresent a directly relevant study that examined cortisol secretion in the saliva of adolescents as a predictor of subsequent development of depression.  It actually found no baseline measure of cortisol measures predicted development of depression except cortisol awakening response.

In general, cortisol secretion is more related to stress than to clinical depression. One study concluded

The hypothalamic—pituitary—adrenal axis is sensitive to social stress but does not mediate vulnerability to depression.

depressed girlWhat is most outrageous about the introduction, however, is the specification of the pathway between having a depressed mother and shortened telomere length:

The chronic exposure of these children to this stress as a function of living with mothers who have experienced recurrent episodes of depression could represent a mechanism of accelerated biologic aging, operationalized as having shorter telomere length.

Recognize the argument that is being set up: having to deal with the mothers’ depression is a chronic stressor for the daughters, which sets up irreversible processes before the daughters even become depressed themselves, leading to accelerated aging, chronic illness, and early death. We can ignore all the characteristics, including common social factors, that the daughter share with their mothers, that might be the source of any daughters’ problems.

This article is a dream paper for the lawyers for men seeking custody of their children in a divorce: “Your honor, sole custody for my client is the children’s only hope, if it is not already too late. His wife’s depression is irreversibly damaging the children, causing later sickness and early death. I introduced as evidence of an article by Ian Gotlib that was endorsed by the Director of the National Institute of Mental Health…

Geraldine Downey and I warned about this trap in a classic review, children of depressed parents, cited 2300 times according to Google Scholar and still going strong. We noted that depressed mothers and their children share a lot of uncharted biological, psychological, and environmental factors. But we also found that among the strongest risk factors for maternal depression are marital conflict, other life events generated by the marriage and husband, and a lack of marital support. These same factors could contribute to any problems in the children. Actually, the husband could be a source of child problems. Ignoring these possibilities constitutes a “consistent, if unintentional, ‘mother-bashing’ in the literature.”

The authors have asked readers to buy into a reductionist delusion. They assume some biological factors in depression are so clearly established that they can serve as biomarkers.  The transmission of any risk for depression associated with having a depressed mother is by way of irreversible damage to telomeres. We can forget about any other complex social and psychological processes going on, except that the mothers’ depression is stressing the daughters and we can single out a couple of biological variables to examine this.

Methods

The Methods lacks basic details necessary to evaluate the appropriateness of what was done and the conclusions drawn from any results. Nonetheless, there is good reason to believe that we are dealing with a poorly selected sample of daughters from poorly selected mothers.

We’re not told much about the mothers except that they have experienced recurrent depression during the childhood of the daughters. We have to look to other papers coming out of this research group to discover how these mothers were probably identified. What we see is that they are a mixed group, in part drawn from outpatient settings and in part from advertisements in the community.

Recall that identification of biological factors associated with depression requires well-defined phenotypes. The optimal group to study would be patients with severe depression. We know that depression is highly heterogeneous and that “depressed” people in the community who are not in specialty treatment are likely to just barely meet criteria. We are dealing with milder disorder that is less likely to be characterized by any of the biological features of more severe disorder. Social factors likely play more of a role in their misery. In many countries, medication would not be the first line of treatment.

Depression is a chronic, remitting, recurrent disorder with varying degrees of severity of overall course and in particular episodes. It has its onset in adolescence or early adulthood. By the time women have daughters who are 10 to 14 years old, they are likely to have had multiple episodes. But in a sample selected from the community, these episodes may have been mild and not necessarily treated, nor even noticeable by the daughters. The bottom line is we should not be too impressed with the label “recurrent depression” without better documentation of the length, severity, and associated impairment of functioning.

Presumably the depressed mothers in the study were selected because they were currently depressed. That makes it difficult to separate out enduring factors in the mothers and their social context versus those that are tied to the women currently being depressed. And because we know that most biological factors associated with depression are state dependent, we may be getting a skewed picture of the biology of these women – and their daughters, for that matter – then at other times.

Basically, we are dealing with a poorly selected sample of daughters from a poorly selected sample of mothers with depression. The authors are not telling us crucial details that we need to understand any results they get. Apparently they are not measuring relevant variables and have too a small sample to apply statistical controls anyway.As I said about another small study making claims for a blood test for depression, these authors are

Looking for love biomarkers in all the wrong places.

Recall that I also said that results from small samples like this one often conflict with results from larger, epidemiologic studies with larger samples and better defined phenotypes. I think we can see the reasons why developing here. The small sample consist only of daughters who have a depressed mother, but who have not yet become depressed themselves and have low scores on a child depression checklist. Just how representative is the sample? What proportion of daughters this age of depressed women would meet these criteria? How are they similar or different from daughters who have already become depressed? Do the differences lie in their mothers or in the daughters or both? We can’t address any of these questions, but they are highly relevant. That’s why we need more larger clinical epidemiologic studies and fewer small studies of poorly defined samples. Who knows what selection biases are operating?

Searching the literature for what this lab group was doing in other studies in terms of mother and daughter recruitment, I came across a number of small studies of various psychological and psychobiological characteristics of the daughters. We have no idea whether the samples are overlapping or distinct. We have no idea about how the results of these other modest studies confirm or contradict results of the present one. But integrating their results with the results of the present study could have been a start in better understanding it.

As noted in my post at Science Based Medicine, we get a sense of the methods section of the Molecular Psychiatry article of unreliability in single assessments of telomeres. Read the description of the assay of telomere length in the article to get a sense of the authors having to rely on multiple measurements, as well as the unreliability of any single assessment. Look at the paragraph beginning

To control for interassay variability…

This description reflects the more general problems in the comparability of assessment of telomeres across individuals, samples, and laboratories problems that, that preclude recommending telomere length as a biomarker or surrogate outcome with any precision.

Results and Interpretation

As in the methods, the authors fail to supply basic details of the results and leave us having to trust them. There is a striking lack of simple descriptive statistics and bivariate relations, i.e., simple correlations. But we can see signs of unruly, difficult to tame data and spun statistics. And in the end, there are real doubts that there is any connection in these data between telomeres and cortisol.

The authors report a significant difference in telomere length between the daughters of depressed women versus daughters in the control group. Given how the data had to be preprocessed, I would really like to see a scatter plot and examine the effects of outliers before I came to a firm conclusion. With only 50 daughters of depressed mothers and 40 controls, differences could have arose from the influence of one or two outliers.

We are told that the two groups of young girls did not differ in Tanner scores, i.e., self-reported signs of puberty. If the daughters of depressed women had indeed endured “accelerated aging,” would it be reflected in Tanner scores? The authors and for that matter, Insel, seem to take quite literally this accelerated aging thing.

I think we have another seemingly large difference coming from a small sample that is statistically improbable to yield such a difference, given past findings. I could be convinced by these data of group differences in telomere length, but only if findings were replicated in an independent, adequately sized sample. And I still would not know what to make of them.

The authors fuss about  anticipating a “dysregulation of the hypothalamic-pituitary-adrenal (HPA) axis and anomalous levels of cortisol secretion.” They indicate that the cortisol data was highly skewed and had to be tamed by winsorizing, i.e., substituting arbitrary values for outliers. We are not told for how many subjects this was done or from which group they came. The authors then engaged in some fancy multivariate statistics, “a piecewise linear growth model to fit the quadratic nature of the [winsorized] data.”  We need to keep in mind that multilevel modeling is not a magic wand to transform messy data. Rather, it involves some assumptions that need to be tested and not assumed. We get no evidence of the assumptions being tested and the small sample sizes is such that they could not be reliably tested.

The authors found no differences in baseline cortisol secretion. Moreover, they found no differences in distress recovery for telomere length, group (depressed versus nondepressed mother), or group by telomere interaction. They found no effect for group or group by telomere interaction, but they did find a just significant (p< .042) main effect for telomere length on cortisol reactivity. This would not to seem to offer much support for a dysregulation of the HPA axis or anomalous levels of cortisol secretion associated with group membership (having a depressed versus nondepressed mother). If we are guided by the meta-analysis of depression and cortisol secretion, the authors should have obtained a group difference in recovery, which they didn’t. I really doubt this is reproducible in a larger, independent sample, with transparently reported statistics.

Recognize what we have here: prestigious journals like Molecular Psychiatry have a strong publication bias in requiring statistical significance. Authors therefore must chase and obtain statistical significance. There is miniscule difference from p<.042 and p<.06 – or p<.07, for that matter – particularly in the context of multivariate statistics being applied to skewed and winsorized data. The difference is well within the error of messy measurements. Yet if the authors had obtained p<.06 or p<.07, we probably wouldn’t get to read their story, at least in Molecular Psychiatry.*

Stay tuned for my next installment in which I compare results of this study to the press release and coverage in Insel’s personal blog.  I particularly welcome feedback before then.

*For a discussion of whether “The number of p-values in the psychology literaturethat barely meet the criterion for statistical significance (i.e., that fall just below .05) is unusually large,” see Masicampo and LaLande (2012)  and Lakens (2015).