by Michael D. Anestis, Ph.D.

I absolutely LOVE it when impressive researchers compare two evidence-based treatments to one another in the same study.  Comparative efficacy is a wonderful thing and we don't get nearly enough of it.  I just came across a great example of this, as Evan Forman, Jena Shaw, Elizabeth Goetter, James Herbert, Jennie Park, and Erica Yuen just published a follow-up to an earlier comparision of cognitive behavioral therapy (CBT) and acceptance and commitment therapy (ACT) in Behavior Therapy, this time reporting results from an 18-month post-treatment assessment point.

In the earlier study, Forman and colleagues (2007) reported that there were no differences between ACT and CBT immediately post-treatment in a randomized controlled trial (RCT) examining a range of outcomes including depressive symptoms, anxiety symptoms, and overall functioning.  This was compelling evidence and supportive of the notion that ACT is a promising emerging treatment capable of producing results comparable to gold standard evidence-based psychotherapy for certain populations.  As the authors noted in this study, however, it is always important to ask not only how folks are doing right after treatment, but also whether or not treatment gains are maintained over time.

The total sample included 132 undergraduates seeking treatment at a counseling center.  Importantly, participants were not required to meet diagnostic criteria for a DSM-IV-TR disorder.  Rather, inclusion criteria centered around moderate levels of depression and/or anxiety as measured by the BDI-II and BAI (scores greater than 9).  In most healthy undergradaute samples I've collected, the mean for the BDI-II comes in around 7, with a standard deviation of 7, so I'm not entirely comfortable with considering 9 a measure of moderate depression symptoms (in fact, "moderate" for the BDI-II is typically defined by a score of 20-28 and the maximum score is 63).  The authors noted that the goal was to keep inclusion criteria broad in order to maximize external validity (e.g., the degree to which the sample and the results reflect what would typically be seen in the "real world").  That's a valid goal, but it is VERY important to keep the context of the sample in mind when interpreting the findings.

As far as diagnoses go, the authors used structured diagnostic interviews and reported that 49.2% met criteria for an anxiety disorder and 37.1%  met criteria for a depressive disorder.

On to the results.  91 participants provided follow-up data and were included in the analyses.  That being said, the authors used both intent-to-treat analyses and a second idetentical set of analyses that only considered the completers.  I'll present the ITT results here.

The authors found that the group of individuals receiving CBT reported greater maintenance of treatment effects for depression and general functioning than did individuals who received ACT.  There was a non-significant trend (p = .08) for quality of life favoring the CBT group and no between group differences on anxiety.  Putting these results in another context, the authors ran analyses considering clinical significance by comparing the percentage of individuals in each group (CBT vs ACT) who were "reliably recovered" on each outcome measure (see the original paper for a thorough description of the meaning of that phrase).  The found the following:

• Depression (BDI-II): 81.8% of CBT patients vs. 60.7% of ACT patients
• Anxiety (BAI): 72.7% of CBT patients vs. 56.0% of ACT patients
• General functioning: 46.4% of CBT patients vs. 22.6% of ACT patients
• Quality of life: 37.8% of CBT patients vs. 22.9% of ACT patients

So, on the whole, the results pain a rather plainly superior long-term outcome for CBT relative to ACT with this particular population, but it is VERY important to keep our understanding of those results within their context.  This is a strong study, but it's only one study.  This is a valid sample, but not a particularly severe one.  The authors used protocols specific to diagnosis, but not everyone had a diagnosis and results for specific diagnoses were not compared to one another here.  Also, the results do not mean that ACT does not work...they simply point towards CBT working better in the long haul.  It will be interesting to see if other studies like this emerge and, if so, whether these results will be replicated. If they are, confidence in their meaning will increase significantly.  In the meantime, this is something to keep in mind.

************

Dr. Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi

Articles cited in this post:

Forman, E.M., Herbert, J.D., Moitra, E., Yeomans, P.D., & Geller, P.A. (2007).  A randomzied controlled effectiveness trial of acceptance and commitment therapy and cognitive therapy for anxiety and depression.  Behavior Modification, 31, 772-799.

Forman, E.M., Shaw, J.A., Goetter, E.M., Herbert, J.D., Park, J.A., & Yuen, E.K. (in press).  Long-term follow-up of a randomized controlled trial comparing acceptance and commitment therapy and standard cognitive behavior therapy for anxiety and depression.  Behavior Therapy.

by Michael D. Anestis, Ph.D.

It's been a while since I last posted on PBB.  Back in mid-May, however, I wrote a piece about suicide in NFL players.  I was moved to write this after reading an article by a former NFL player discussing his own experiences and, towards the end of the post, I mentioned that chronic traumatic encephalopathy (CTE) has been the subject of significant recent research and is another important cause to consider with respect to deaths by suicide within this population.  I made this last point in large part due to substantial news coverage on the topic, which had reported that CTE - which can only be diagnosed post-mortum through an autopsy - had been found in a substantial number of professional athlete suicide decedents.  Now, my background in neuroscience is a bit lacking, so I want to preface this piece with a very clear statement that I have much to learn about the science underlying CTE and other medical conditions related to the brain; however, I felt compelled to write another piece today to share some surprising information I've come across in the past week or so.

In a casual conversation with a colleague, Joye heard about recent research presented by Dr.Christopher Randolph at the 2012 American Academy of Clincal Neuropsychology conference that called into question the validity of the CTE diagnosis.  I then emailed Dr.Randolph, who sent me the slides from his presentation and granted permission for me to discuss them here.  Dr.Randolph's presentation touched on a number of topics beyond CTE, but I want to focus this post specifically on this aspect of what he said.  Almost all of this information comes directly from his slides.

Dr.Randolph mentioned that the first reference he could find to CTE was in an article published by Omalu and colleagues in 2005 in which the authors discussed the results of an autopsy (physiological and psychological) that indicated that an NFL player who had died at age 50 from a heart attack had previously displayed symptoms consistent with dysthmia, memory and judgment deficits, and parkinsonian symptoms.  Most interestingly, however, the authors noted that the decedent's brain exhibited "diffuse amyloid plaques" and "sparse neurofibrillary tangles (NFT's)" but that his brain was otherwise quite normal.  The authors indicated that a diagnosis of CTE was warranted.

The authors did not present any specific criteria for CTE or any population-based comparisons that would enable a better understanding of the degree to which the abnormalities noted in the decedent's brain truly differed from the general population.  They did, however, list a number of possible symptoms of CTE, including mood disturbances, dysregulated behavior, difficulty concentrating, paranoia, and disturbances in movement.

Omalu and colleagues (2006) followed up that original study with another discussion of a former NFL player, in this case one who had died by suicide after intentionally ingesting antifreeze.  In this case, the decedent had experienced three prior psychiatric hospitalizations and an examination of his brain revealed no diffuse amyloid, but NFTs in "several regions." 

In 2009, McKee and colleagues presented three new cases, one a former NFL player (age 45) who died accidentally, one a retired boxer (age 80) who died of septic shock and had experienced progressive dementia (without formal diagnosis), and another retired boxer (age 73) who died of pneumonia after apparently suffering from progressive dementia.  Here again, the authors claimed to find evidence of CTE across all cases; however the only commonality across the decedents was the presence of NFTs.  Furthermore, the authors concluded that the total number of "neuropathologically verified" cases of CTE in the literature was now 51, including 48 other cases in the literature dating back to 1954 and including all deaths previously classified as dementia pugilistica. This is a surprisingly powerful statement given some fairly mixed results and a very limited sample across studies.

At this point in his presentation, Dr.Randolph noted that a diagnosis of CTE appears to only require the presence of NFTs somewhere in the brain.  As somebody with little background in neuroscience, I can look at a sentence like that and be completely unsure whether or not that constitutes a problem; however, Dr.Randolph clarified that quite well by presenting relevant findings from Bennett and colleagues (2006).  Using a sample of 134 individiduals who were examined prospectively and who were cognitively normal at the time of death, the authors found that 97% exhibited NFTs.  In other words, almost the entire sample had NFTs even though they exhibited no behavioral or cognitive difficulties at the time of death.

Now, does that mean that all NFTs are the same?  No.  Does it mean that the presence of NFTs can't serve as a vulnerability to particular outcomes (e.g., suicidal behavior) within the context of other risk factors?  Of course not.  But it does mean that finding NFTs in the brain of a deceased individual might not be enough to justify a diagnosis that can then be used to "explain" a behavioral outcome like death by suicide.

In my opinion, the most intriguing point raised by Randolph throughout this presentation (which is saying a lot, actually, as I found the entire thing rather enlightening) came from a reference to a study conducted by Baron and colleagues (2012).  Using a sample of 3,439 NFL players with at least 5 pension-credited seasons between 1959 and 1988, they found that fomer NFL players had a rate of death by suicide that was only 41% of that of the general population.  In other words, NFL players were significantly LESS likely to die by suicide than were individuals who did not play in the NFL.  Now, its entirely possible that the rate has changed in players with more recent careers or that deaths by suicide were classified as something else within that sample, but the evidence presented there in a rather large and representative sample directly contradicts the notion that suicide has become a near epidemic within the ranks of retired players.

I want to be very careful to ensure that I'm clear here.  I'm not saying that suicide within the NFL is not a problem or that brain injuries can not significantly impact behavior and mood.  In fact, I'm not saying the CTE doesn't exist (and I don't believe Dr.Randolph is either, necessarily).  In fact, Dr.Randolph has published plenty of data linking head injuries to dementia.  What I am saying, however, is that suicide is not an epidemic within the NFL.  It happens, and likely for the same reasons it happens elsewhere, with some differences that I outlined in my previous post on this topic.  Furthermore, I'm saying that research on CTE needs to result in greater specificity in terms of diagnostic criteria and there needs to be a greater degree of replication across studies before we place such a huge emphasis on using CTE as a blanket explanation for tragic outcomes that befall current and former professional athletes.

I would love to hear your thoughts on this, particularly if you have a neuroscience background.

************

Dr.Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississppi

Articles cited in this post:

Baron, S.L., Hein, M.J., Lehman, E., & Gersic, C. (2012).  Body mass index, playing position, race, and the cardiovascular mortality of retired professional football players.  American Journal of Cardiology, 109, 889-896.

Bennett, D.A., Schneider, J.A., Arvanitakis, Z.Z., Kelly, J.F., Aggarwal, N.T., et al. (2006).  Neuropathology of older persons without cognitive impairment from two community-based studies.  Neurology, 66, 1837-1844.

McKee, A.C., Cantu, R.C., Nowinski, C.J., Hedley-Whyte, T., Gavett, B.E., et al. (2009).  Chronic traumatic encephalography in athletes: Progressive tauopathy after repetitive head injury.  Journal of Neuropathology and Experimental Neurology, 68, 709-735.

Omalu, B.I., DeKosky, S.T., Minster, R.L., Kamboh, M.I., Hamilton, R.L., et al. (2005).  Chronic traumatic encephalopathy in a National Football League player.  Neurosurgery, 57, 128-134.

Omalu, B.I., DeKosky, S.T., Hamilton, R.L., Minster, R.L., Kamboh, M.I., et al. (2006).  Chronic traumatic encaphalopathy in a National Football League player: Part II.  Neurosurgery, 59, 1086-1092.

Randolph, C. (2012).  Long-term consequences of sport-related concussion/repetitive head trauma.  Research presented at the American Academy of Clinical Neuropsychology annual conference.  Seattle, WA.

by Michael D. Anestis, Ph.D.

The other day, a friend of mine shared a link to an ESPN story written by former NFL linebacker George Koonce in which he courageously shared his story of struggling to adjust to post-NFL life.  This is a topic that I've thought about from time to time in the past and which was already on my mind in the wake of Junior Seau's recent death by suicide and I wanted to take the opportunity today to write a bit about it and to hear your thoughts on the issue.

Before getting into the specifics of this particular situation, let me quickly refresh your memory on the Interpersonal-Psychological Theory of Suicidal Behavior (IPTS; Joiner, 2005).  I've written about this a ton on PBB, as I was trained by Dr.Joiner and the theory is a core feature of my own research (click here for our initial article on this), but it's worth setting the stage for this by quickly outlining the key components.  The theory points out that there is an important difference between the desire to die by suicide and the ability to die by suicide - that the vast majority of those who want to die by suicide can't and the vast majority of those who could do not want to do so. 

The desire is said to be comprised of two variables: thwarted belongingness and perceived burdensomeness.  Thwarted belongingness is a sense on the part of an individual that he or she lacks meaningful connections to others - either that others do not care about them or that although others care they do not fully understand them, thereby leaving a sense of distance.  Perceived burdensomeness is a sense on the part of an individual that he or she makes no meaningful contributions to the world - that their death would be worth more than their continued life.  When both of these variables are present, and particularly when an individual feels hopeless about these two issues, the desire for suicide becomes much more likely (see Van Orden et al., 2010 for a summary of the data supporting the IPTS).

The ability for suicide is a bit more of an unusual idea.  At its core, the idea behind this variable is that we are not inherently capable of killing ourselves.  The will to live is woven into our genes and the drive to survive makes inflicting lethal self-harm remarkably difficult.  This, in large part, explains why there are somewhere between 8.5 and 25 non-fatal suicide attempts for every death by suicide and an enormous number of individuals who desire death by suicide but never attempt.  Taking it a step further, Joiner's point here is that suicidal behavior is both terrifying and physically painful/uncomfortable and that, in order to engage in serious or lethal suicidal behavior, an individual must develop the ability to tolerate great amounts of physical pain and to overcome the fear of death/bodily harm.  What research has shown is that this habituation process occurs through repeated exposure to painful and/or provocative events (PPEs).  PPEs can be a lot of things.  They could be repeated episodes of non-suicidal self-injury, witnessing death/physical injuries in others, or even experiencing flashbacks of injuries you've had in the past (e.g., Anestis et al., in press; Joiner et al., 2009).  Keep these points in mind as you read this and consider how they might be relevant to NFL players transitioning into post-NFL life.

One of the main issues discussed by Koonce is one that I have been talking about with colleagues quite a bit and a point I've seen discussed in various media outlets as well: adjusting to life after the NFL is an extreme struggle for some players.  When I think about that transition, I tend to see a parallel with the situation experienced by soldiers reintegrating into civilian life post-deployment.  Now don't get me wrong here - this is not another misguided comparison of football to war.  Not at all.  The overlap I see isn't one in which they are all "soldiers."  Rather, much like military personnel deployed in OIF/OEF, NFL players spend a portion of their life sharing an experience that differs greatly from that of most Americans.  It is an insulated culture in which they have a clear membership and purpose and are celebrated for that reason.  As Koonce says in his article, football becomes their identity and, in that sense, they share a bond with other players that would be difficult for any of us not involved in that experience to fully grasp.  They train relentlessly to perform their duties and then, one day, they're done.  Suddenly, for a lot of them purpose and group membership are a lot less clear.  Certainly many of them have families that love them dearly, but those family members likely did not share the NFL experience and, in that sense, the former players may still feel somewhat distant.  Think back to my description of thwarted belongingness and perceived burdensomeness...see any relevance here? 

Now, that particular aspect of the NFL experience isn't altogether different from a lot of professions.   A lot of people are a bit adrift when they transition out of an experience around which they've built much of their identity.  In fact, men over the age of 65 have the highest rate of death by suicide of anyone - signalling that retirement may, in fact, serve as a risk factor for some.  The thing is, NFL players retire MUCH younger than most of us do.  In a lot of ways, this sounds (and in many cases, is) wonderful, but that no doubt depends upon the individual.  In  some ways, it might simply push a risk factor typically applied to older adults (or to young soldiers suddenly thrust back into the life of a civilian) to a younger age bracket.

Another issue that sets former NFL players apart from others (and strengthens the parallel to military service), however, is in the likely impact of their chosen career on the acquired capability for suicide.  Playing football involves years of physically demanding and painful experiences.  Players put their bodies at risk every time they step on the field, every time they make a catch across the middle, lower their shoulders to make a hit, or step in front of a blitzing linebacker to protect the quarterback.  The very nature of their job requires them to absorb immense amounts of physical punishment and to develop the ability to not only tolerate the pain, but overcome the fear of experiencing physical harm.  Here again, a parallel to military service is strong.  We've published data showing that US Air Force personnel who recently completed basic training reported higher levels of the acquired capability than did civilian clinical and non-clinical samples.  Certain jobs require you to experience pain differently and to recalibrate your response to risk.  That adjustment is pivotal for the survival of those in those jobs while they are involved in the job itself and, in and of itself, the adjustment is not problematic.  The question, however, is what happens if those folks develop suicidal desire. It may be easier for former NFL players to act on suicidal desire, particularly with respect to lethal means, than it is for individuals whose lives have not involved so much pain and provocation.

My point here is not to say that military service or professional football are bad.  Quite the opposite, actually.  My point, rather, is to say that, given the inherent risks associated with playing football, steps need to be taken in order help former players enhance their sense of purpose and belongingness after their playing days are over.  This could involve a multitude of options, but involving former players in the league somehow (through NFL charities, some sort of former NFL players golf tour, etc...) could serve to ease that transition a bit and keep vulnerable individuals from getting stuck in a cycle that ultimately results in the desire for death.

I would give almost anything to actually collect data on NFL players and alums to measure these ideas, but that is likely impossible, so it is important to keep in mind here that my thoughts on these issues are just thoughts and not empirically-based opinions.  Thinking about things in this way, however, seems more useful to me (and certainly more solution-oriented) than simply looking at former players and shaking your head at them because you think having lived a life of celebrity and wealth should make it easy to overcome life transitions that are inherently difficult.

I would be interested in hearing your thoughts on this.  Certainly I have not mentioned CTE here at all and that's a relevant issue to consider (and not one that is in any way inconsistent with these ideas).  What else do you think plays a role here?  What should be done?

************

Dr. Mike Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi

Sources cited in this post:

Anestis, M.D., Tull, M.T., Bagge, C.L., & Gratz, K.L. (in press).  The moderating role of distress toelrance in the relationship between posttraumatic stress disorder symptom clusters and suicidal behavior among trauma-exposed substance users in residential treatment.  Archives of Suicide Research.

Joiner, T.E. (2005).  Why people die by suicide.  Cambridge, MA: Harvard University Press.

Joiner, T.E., Van Orden, K.A., Witte, T.K., Selby, E.A. Ribeiro, J., Lewis, R., & Rudd, M.D. (2009).  Main predictions of the interpersonal-psychological theory of suicidal behavior: Empirical tests in two samples of young adults.  Journal of Abnormal Psychology, 118, 634-646.

Van Orden, K.A., Witte, T.K., Cukrowicz, K.C., Braithwaite, S.R., Selby, E.A., & Joiner, T.E. (2010).  The interpersonal theory of suicide.  Psychological Review, 117, 575-600.

by Michael D. Anestis, Ph.D.

DSM-V is certainly in the news these days.  Recently, the folks responsible for developing the forthcoming new edition of the diagnostic manual announced that they were backing off their plans for two potential new diagnoses, a decision that was met with widespread applause.  Now, Allen Frances has reported that, at the annual APA convention, data regarding the reliability of the proposed diagnostic structure for DSM-V from the field trials are now available and the results are....horrifying.

A little history here.  In the first two editions of the DSM, diagnoses were generally described in vague terms that emphasized symptoms that were difficult to assess and measure with any consistency.  In this sense, the writers of the early manuals did not place much of a premium on reliability, which in this particular sense refers to the degree to which two clinicians who assess the same patient will agree on the presence or absence of a particular diagnosis.  When DSM-III came around, psychodynamic jargon and other unclear phrasing was removed and a heavy emphasis was placed on behavioral indicators and other symptoms that could more reliably measured.   In doing this, they vastly increased the reliability of the diagnoses in the manual, although some feared that, as a result, they decreased the validitiy (in this case, validity refers to the degree to which the diagnosis as described actually represent the diagnosis as it occurs in reality).  To some extent, increasing reliability can require a decrease in validity (e.g., I might removed a confusing criterion that truly is a part of the disorder in order to increase the likelihood that people will agree whether or not somebody has that disorder).  This is a particularly important issue to consider with the present controversy.

Back to the present.  Dr.Frances reported that the kappa values - a measure of agreement between clinicians as to whether or not an individual meets criteria for a diagnosis - were just awful for a large number of disorders.  For instance:

• Depression - kappa = .32
• Generalized anxiety disorder - kappa = .2
• PTSD - kappa = .67
• Autism spectrum disorder - kappa = .69
• Antisocial personality disorder - kappa = .22
• Obsessive-compulsive disorder - kappa = .31

To give some context to those numbers, kappas of .4 have historically been considered "poor," and, indeed, the results of the DSM-III field trials left the authors of that decision confident that kappas below .6 would be a cause for concern (Spitzer, Williams, & Endicott, 2012).  Frances put forth a number of potential explanations for the problematic data for DSM-V diagnostic categories.  Amongst his arguments were:

• Nobody on the DSM-V committees was capable of developing clearly worded and succint diagnostic criteria and, as such, the wording was a recipe for disaster (and the results forseeable)
• The complexity of the procedures involved in the DSM-V field trials was over the top, again setting folks up to fail
• A second stage of the field trials in which poor data would be addressed through revision and further data collection was canceled due to timing and financial issues (as well as the need to meet publication deadlines).

From what I've read, there is near universal concern about these results within the field.  Some authors have noted that traditional standards for kappa evaluation are unrealistically high and that the new diagnoses might need to sacrifie some reliability for validity (e.g., Kraemer, Kupfer, Clarke, Narrow, & Regier, 2012).  Looking at these numbers, however, you have to wonder whether too much of one is being sacrified for unknown levels of the other.

Issues like this concern me for a number of reasons.  First, the obvious.  It doesn't look good for our field when, in an effort to enhance the scientific and clinical value of our diagnostic system, we create a system that yields chaotic levels of disagreement amonst clinicians regarding whether or not a particular disorder is present.  Nobody expects perfection on that front, but we need to not be lowering the bar at this point.  Second, I feel as though this might increase the strength of calls to abandon diagnostic systems entirely.  Although I obviously sympathize with the sentiments behind not "labeling" folks who are struggling, a properly developed and implemented diagnostic system doesn't do that.  What it does is create a single language that all researchers and clinicians can speak with respect to the presentations of individuals struggling with mental illness.  Doing this allows for systematic research on particular treatments, trajectories of particular symptom clusters, and other important issues, thereby enabling accountability with respect to what clinicians should and should not do for their clients.  Although a poor diagnostic system will pathologize normal processes, a lack of diagnostic system will result in chaos (e.g., without a diagnosis, which treatment will be used and how will we assess success and to whom will the results of such treatments be compared?).  In a sense, I see this almost as an argument to strive for a good government rather than choosing anarchy when the government proves imperfect.  We need a system within which to work - the fact that so many individuals out there practice sham treatments even WITH data pointing towards better options should speak clearly to our inability to function effectively without guidelines.  Don't get me wrong here, - I'm not suggesting that this outcome is anywhere close to happening.  I just think that missteps like this result in increased energy being spent on issues unlikely to move us forward, so in the end, we all lose.

DSM-V is not a simple issue and a lot of brilliant and well-intentioned people vehemently disagree on these issues. How this all plays out will have an enormous impact not only on those of us working within the field, but everyone in the world who struggles with mental illness.

************

Dr. Mike Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi

Articles cited in this post:

Kraemer, H.C., Kupfer, D.J., Clake, D.E., Narrow, W.E., & Regier, D.A. (2012).  Response to Spitzer et al letter.  American Journal of Psychiatry, 169, 537-538.

Spitzer, R.L., Williams, J.B.W., & Endicott, J. (2012).  Standards for DSM-5 reliability.  American Journal of Psychiatry, 169, 537.

by Michael D. Anestis, Ph.D.

The remarkably controversial development of DSM-V took another major turn with the revelation that two proposed changes are now being dropped (click here to read a summary).  Both Attenuated Psychosis Syndrome and Mixed Anxiety Depressive Disorder have been removed from consideration as new diagnoses.  I don't have time to reflect much on these changes this morning, but wanted to share the link and invite your thoughts on this shift and others you'd like to see in the forthcoming diagnostic manual.

************

Dr. Mike Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi

by Michael D. Anestis, Ph.D.

Earlier today, when I learned about the death by suicide of former NFL linebacker Junior Seau, I decided it would be worthwhile to write a quick post on interesting new findings related to suicidal behavior.  None of the findings below are directly related to this story, but in the spirit of raising awareness, I thought there might be some value in quickly summarizing a couple of cool effects that I came across in the current issue of Suicide and Life-Threatening Behavior.  We've discussed similar findings in the past, but replication is remarkably important in science and, as such, I chose to bring these studies up on PBB.

Interesting finding #1:

I've discussed this issue at length in the past (link, link), but its importance cannot be overstated.  There is an understandable and widely held belief that talking to people about suicide might increase their risk for thinking about or even engaging in suicidal behavior.  A growing number of studies have not only debunked this myth, but have acutally shown that the opposite is true: that asking about suicide appears to decrease levels of suicidal ideation, particularly in high risk samples. 

In a study in the current issue of SLTB, Chrarles Mathias and colleagues (2012) recruited 170 adolescents (age 12-17; 50% male; 57% Hispanic) who had experienced psychiatric inpatient care.  Participants were assessed for suicidal ideation at baseline and then again every six months for up to two years.  Suicidal ideation was assessed using a self-report questionnaire.  Of the 170 participants, 159 completed the second assessment, 126 completed the third, 77 completed the fourth, and 54 completed all five.  Three of the lost participants were missing due to attrition (e.g., did no return for an appointment).  The remainder were missing due to the fact that their initial assessment occurred late enough in the project that the project had ended before they could have completed all time points.  In other words, the missing data should not be seen as a sign that individuals were becoming increasingly severe and dropping out of the study due to that increased severity. 

What did they find?  First off, a greater number of assessments was associated with lower suicidal ideation in the final assessment, even after accounting for initial levels of suicidal ideation.  In other words, not only did asking about suicidal ideation once no cause an increase in thoughts of suicide, but asking repeatedly was actually associated with continuingly decreasing levels of ideation.  In total, 51% of the participants reported a decrease in ideation during the study, 29% reported no change, and 21% experienced an increase from their first to final assessment.  Furthermore, amongst those who reported decreases in ideation, substantially more reported large decreases than moderate or small decreases.  On the flip side of that coin, amonst those who reported increases, more reported small increases than moderate or large increases (the difference between small and large was not statistically significant, however).

Using more comprehensive model testing procedures, the authors found that individuals who reported low levels of ideation at the onset of the study tended not to experience meaningful increases in ideation in response to repeated assessments.  Indviduals with moderate levels of ideation typically reported a decline in ideation between the first and second assessments, but no significant change beyond that point.  Perhaps most importantly, individuals who initially reported high levels of ideation typically reported sharp declines in ideation during the first year, followed by a less steep decline in year 2.

There were several other interesting findings in this study, but the take home message is clear and entirely consistent with prior work on this topic: assessing for suicide risk is not only safe, but beneficial, particularly with high risk individuals.  In other words, there is substantial potential value and no discernable risk with the institution of wide spread suicide risk assessment protocols.

Interesting finding #2:

In our past discussions of the interpersonal-psychological theory of suicidal behavior (IPTS), we have discussed the importance of thwarted belongingness as a driving force behind suicidal desire.  Put simply, when individuals feel as though they lack meaningful connections to others, the likelihood that they will desire death by suicide increases substantially.  In many cases, efforts to decrease thwarted belongingness focus on close individuals bonds and understandably so.  That being said, such relationships are not the only path towards increasing an individuals sense of belonging.  A couple of years ago, I discussed work examining the relationship between professional sporting events and suicidal behavior (link) and a study in the current issue of SLTB replicated the effects noted in that earlier PBB article.

Specifically, Gaelle Encrenaz and colleagues (2012) examined the association between the 1998 World Cup and monthly deaths by suicide in France.  Controlling for the effects of variables like seasonality (e.g., deaths by suicide peak in the spring), the authors found that, between June 11th and July 11th of 1998, there was a decrease of 95 deaths by suicide - a 10.3% decrease from the norm.  Furthermore, they found a decrease of 19.9% on days following games (victories, in this case) by the French team.

Do these findings mean that the occurance and associated outcomes of sporting events are amongst the most important variables to consider in suicide resarch?  Of course not.  What they indicate, however, is that events that cause us to feel connected to a group make us feel very differently about ourselves and, perhaps most importantly, about our death.

************

Dr. Mike Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi.

Articles cited in this post:

Encrenaz, G., Contrand, B., Leffondre, K., Queinec, R., Aouba, A., Jougla, E., Miras, A., & Lagarde, E. (2012). Impact of the 1998 Football World Cup on suicide rates in France: Results from the National Death Registry.  Suicide and Life-Threatening Behavior, 42, 129-135.

Mathias, C.W., Furr, R.M., Sheftall, A.H., Hill-Kapturczak, N., Crum, P., & Dougherty, D.M. (2012).  What's the harm in asking about suicidal ideation? Suicide and Life-Threatening Behavior, 42, 1-11.

by Michael D. Anestis, Ph.D.

A few days ago, the New York TImes published an article in their Sunday Review entitled "Is therapy forever? Enough already."  The title was exciting, as it seemed to indicate that the piece might explain that scientific evidence supports the efficacy and effectiveness of a number of time-limited, manualized treatments for specific diagnoses.  Yes! Science leaking through the pages of the Times rather than empty pro-psychoanalysis rhetoric!

Sadly, I was disappointed.  Although the piece has been spoken about positively by a number of people for whom I have immense amounts of respect, it seemed to lump all forms of therapy together as one, spoke vaguely about "aggressive" therapists, and generally oversimplified the entire process, leaving individuals in need of help with no sense of how to differentiate between evidence-based and experimental (or worse) forms of treatment.  In fact, the only specific information was about the services provided by the author himself.

Things took a turn for the worse today, however, when I was directed to a retort published on Forbes.com in which a proponent of long-term psychotherapy blindly cited widely discredited (or least HIGHLY controversial) studies published in the Journal of the American Medical Association, the British Journal of Psychiatry, and the American Psychologist, which we have addressed at length on this site (click here, here, and here for examples) - even referring to Shedler's unfortunate piece as an "instant classic."  These studies claim to show that long-term psychotherapy is superior to short-term psychotherapy and that psychodynamic psychotherapy is not only effective, but more so than cognitive behavioral therapy.  The writer did this without mentioning the controversy surrounding those articles, which is more than a little ironic given that he cited them in a sentence in which he was accusing somebody else of cherry picking evidence.  The writer did have some interesting comments regarding the manner in which the Times writer represents himself on his website, but ultimately his piece was simply another regurgitation of fautly evidence that supposedly supports the use of his favored form of treatment and which perpetuates the problem of ever-present unvalidated treatments for mental illness by once again being spoonfed to a large audience of readers who have no way of knowing the degree to which the words they are reading run counter to reality.

My point here is not simply to point out to you that two more bad articles have been sent into highly cyberspace on sites with heavy readership, but rather to issue a call to arms to scientists with any interest in seeing the public benefit from their amazing work rather than continuing to fall into the trap of buying the messages of charlatans.  Please - as often as you can - write articles for major newspapers and/or websites.  Please, join Twitter or some other social media site and send out links to articles (or pages that explain them in easier to understand terms).  Please post educational videos on YouTube or given presentations to local groups seeking to learn about mental illness and its treatment.  Please, appear on television, no matter how ridculous the program, and explain what it is you do, why it is so important, and how the messages people hear about mental health through the media are almost always completely wrong and often actually dangerous.  That type of work does not get any of us closer to tenure and, given that this is my first post on PBB in a month, clearly I put significantly more focus into my own research than I do into this type of thing as well, so I'm not pointing fingers here.  I'm simply saying that an organized effort on the part of scientifically-minded psychologists to actually try to get their message more publicity and counter the ever-present voice of non-scientifically-minded salesmen would have the potential to benefit a huge number of people.  Any effort helps.

************

Dr. Mike Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi

Thought I'd take a moment to share a PSA by my graduate school major professor, Thomas Joiner.  This kind of thing is not done nearly enough by prominent researchers, but it's a great way to spread hopeful and important messages to folks in need who might not otherwise have access to this information.  Good stuff!

************

Dr. Anestis is an incoming Assistant Professor in the Department of Psychology at the University of Southern Mississippi

by Michael D. Anestis, Ph.D.

This is not a political forum and I'm definitely not looking to incite any sort of contentious conversation about political leanings.  That being said, let me open this up by making clear that I am about as pro-free speech as an individual can get.  Ok...that that's out of the way, I pose a bit of a dilemma:

In a country in which we believe that everyone is entitled to free speech, does the media have an obligation to filter out opinion pieces on mental health related topics that stray from the facts?  In other words, would quality control that prevents people who are likely well-intentioned and intelligent but who do not to have a handle on the facts from being granted vast stage upon which to rant errouneously about topics that have legitimate life-or-death consequences for readers violate our basic First Ammendment rights?  It's a tricky question, but I wonder whether the answer lies not in restricting the speech of such folks, but rather improving the ability for that speech to become a conversation (e.g., pieces that counter-balance opinions with facts, comment sections that are not closed after the first 15 comments).

Anyway, I raise this point in response to yet another horrific mental health article in the New York Times (click here to read the article) - a paper that, on the whole, I love, but which routinely enrages me with their willingness to continuously barrage their enormous readership with patently false information regarding mental illness and its treatment.  Today, another in a long line of mental health articles written by somebody without any (to my knowledge) advanced degree in the field discussed the author's beliefs that:

• All psychotherapies can be uniformally grouped into the term "talk therapy"
• That psychotherapy involves lying on a couch and discussing feelings
• That psychotherapy is no longer common
• And here's the most absurd of them all: that creating writing seminars are a suitable replacement for psychotherapy

This kind of thinking, while I'm sure well-intentioned and based on compelling anecdotes, is just remarkable in its level of absurdity.  It's not just that stuff like this is wrong: it is (1) dangerous and (2) unethical.  Both the danger and the lack of ethics stem from the fact that people in need of help can read this sort of drivel and become convinced that creative writing is, in fact, the best solution for their mental illness.  In doing so, they will have been steered away from effective care, potentially putting their lives in danger.  If somebody steered people away from effective care for cancer or any other physical ailment, there would be an outcry about the snake oil salesmen trying to lure vulnerable people into false hope when real hope already exists.  When it happens with mental illness, however, many people seem to hold onto a strange belief that it is suddenly okay. 

This is a problem and the New York Times needs to look in the mirror and reconsider it's values when it comes to publishing information on mental health.  These aren't philosophical matters of little consequence.  These are issues battled daily by scientists and which have a direct impact on the life (and death) of countless individuals.

************

Dr. Mike Anestis is an incoming Assistant Professor in the Department of Psychology at the University of Southern Mississippi

by Michael D. Anestis, Ph.D.

As is so often the case, the listserv for the Society for a Science of Clinical Psychology (SSCP) recently brought my attention to an interesting and highly important story: the saga of attempts by researchers to publish replication studies (particularly when such studies do not report results consistent with the original study).

To explain why I think this issue is both important and interesting, let me start by explaining what I mean by replication and then explain why it is so pivotal in science.  Any time a scientist conducts a study, analyzes his or her data, and publishes the results, there is always the possibility that the findings were due purely to chance.  Generally speaking, good hypotheses are driven by theory and build off of prior findings, which lowers (although does not eliminate) our concern that a result might not be real.  Every now and then, however, a researcher publishes a controversial result and concerns that the results are not real skyrocket.   The best way to address those concerns is replication.  Rather than simply debating the potential truth of a claim, scientists test it by following the same procedures of the original researcher and attempting to replicate the results.  The more often a result can be replicated independently (in the absence of repeated failures to replicate) the more confident we become that the original effect was real.  By doing this, we don't "prove" anything to be true, but we increase our confidence that we are thinking about things in a way that accurately reflects reality.  This is a big big deal.

Now...the fact that something is a big deal does not make it popular.  As it turns out, it is extremely difficult to publish pure replications.  If a researcher replicates an effect in the process of also testing something else or adding another dimension to the study, the process becomes easier; however, if they deviate from the original plan that way, it also becomes easier for the original researcher to shrug off failures to replicate by noting that the new experiment did something different.  So...in order to remain employed, gain tenure, and thrive professionally, researchers need to continue to publish regularly, but in order to replicate controversial findings and further our understanding of the validity of those effects, researchers would have to invest their time and efforts into a process unlikely to yield results that help them professionally.  That's not ideal.

The reason this came up on SSCP goes back to a story last year, when Dr. Daryl Bem of Cornell University published a series of nine studies that he claimed were supportive of precognition in the highly prestigious Journal of Personality and Social Psychology.  Needless to say, these results were met with substantial skepticism and, accordingly, some researchers were willing to take on the difficult and potentially not so rewarding task of trying to replicate the results.  As it turns out, multiple researchers have now successfully published failures to replicate Bem's original findings, which is unsurprising to those of us who found the original results counter-intuitive, and highly important in that it put our skepticism to the empirical test.  What's really interesting, however, is how difficult it was for researchers to get these important results through the filter of the publication process.

To help illustrate what the process was like, I'm including a link to an article by Chris French of the University of London, who was the lead author of one of the now published failed replication efforts.  The article is a really interesting account of what it was like to get these results where they are now and a commentary on the role of replication in science:

Chris French article

For those of you interested in reading the results themselves, you can read them here (they are published in PLoS ONE, a high impact, open access journal).

I've seen a number of potential solutions offered as ways to overcome the obstacles associated with publishing replications.  That being said, what do you think would be the best answer?  Do we even need one?

************

Dr.Anestis is an incoming assistant professor in the Department of Psychology at the University of Southern Mississippi