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).

2 thoughts on “NIMH Biomarker Porn: Depression, Daughters, and Telomeres Part 1”

  1. Where is the HPA axis dysregulation? It is mainly in the minds 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.

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  2. Thanks, Dr. Carroll for weighing in and leaving no doubt of your take on claims about the HPA axis in this article.

    I was prompted by your comment to think more about the article. I now realize that the authors first made claims that daughters of depressed mothers had their HPA axis dysegulated by exposure to their mothers experience of depression. That would seem to require simple, main effect differences from controls in in the various cortisol measures. None were found, so they simply moved on to distracting us with the analyses involving telomere length. Quite a slight of hand except, has you point out, there was really nothing there either.

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