I no longer support genetics research into eating disorders. Okay, that’s not quite right: I no longer support genetics research into eating disorders under the pretense that it will improve treatment outcomes or prevent eating disorders. I just don’t believe it. Moreover, I think emphasizing the need for a genetic understanding of eating disorders shifts focus away from research and, more importantly, from actions, that can yield much greater benefits much quicker.
It wasn’t always like this. In my third (junior) year of university, I wrote a mini-review on the genetic and neurobiological etiology (cause) of anorexia nervosa. In it, I argued that “in order to improve recovery outcomes, more specific treatments based on genetic and neurobiological evidence need to be developed.” I concluded by writing,
However, with the advent of large-scale genetic databases and worldwide collaboration among researchers resulting in larger sample sizes, the future of AN research is hopeful. These studies are important in order to develop a comprehensive understanding of AN etiology and develop targeted, specific, and effective treatment programs.
I wrote that in 2008. Since then, I have learned more about eating disorders, genetic and neurobiological research, social determinants of health, and various health care systems. I also became aware of and began to learn more about the relationship between scientific research, mental health treatment, and neoliberalism. The more I learned, the less I believed that genetic research into eating disorders would significantly improve treatment outcomes or prevent eating disorders.
Will it help us develop personalized and effective treatment programs? Maybe in the future, but who — and how many — will have access to these treatment programs?
Is there an easier, simpler, more cost-effective way to improve outcomes? And will genetic research into eating disorders tell us something we don’t know that we can use in order to improve outcomes or will it just confirm what we already know or what we can ascertain through less expensive, less complex means?
Below, I outline some reasons for why I no longer support genetics research into eating disorders. If this wording is too strong, let’s just say I am highly skeptical of the assumption that genetics research into eating disorders is required to improve outcomes.
My perspective is important for context: I am writing as someone with lived experience of an eating disorder and with some limited knowledge in neuroscience and genetics. My undergraduate degree was in neuroscience; I completed my Master’s degree in a molecular genetics lab. Importantly, my opinions are not fixed. I am open to change, I am open to debate, and I am always happy to learn.
I worry that emphasizing the need to understand the genetic basis of eating disorders shifts the focus from doing what we already know will likely improve outcomes for people with eating disorders.
By arguing that we need to understand the genetic basis of eating disorders to improve treatment outcomes or prevent eating disorders, we are ignoring the vast body of literature that already provides us with a multitude of suggestions on how we can improve outcomes for people with eating disorders.
While the literature on predictors of positive treatment outcomes is conflicting, we know that early intervention is important because shorter illness duration, less severe symptoms, and higher BMI at treatment start are frequently found to predict positive treatment outcomes; an early response in treatment is also important (Ben-Tovim et al., 2001; Buhren et al., 2013; Fichter, Quadflieg, & Hedlund, 2006; Lo Sauro et al., 2013; Steinhausen, 2002; Vall & Wade, 2016; Wales et al., 2016).
Research also shows that individuals experience a wide range of barriers in accessing and utilizing treatment. In a recent article, Thomspon and Park (2016) outline some of the barriers to accessing and utilizing eating disorder treatment among women. In addition to health beliefs and personality traits, barriers to accessing treatment include financial cost, long waitlists, physicians’ beliefs (i.e., not recognizing eating disorders), social stigma, and distance from treatment centers, among others.
In 2011, Hart and colleagues published a systematic review illustrating a substantial unmet need for treatment among people with eating disorders. Overall, they found that less than a quarter of individuals sought treatment. This is based on fourteen studies, only one of which reported treatment seeking in males, only two reported on individuals above 45 years of age, and only two reported on participants under 18. So, there’s no doubt in my mind that the true proportion is even lower.
This is even more upsetting:
All of these studies reported that although a majority of cases believed they needed treatment, and a number sought to engage in treatment, only a small minority ever received it. For example in the Cachelin et al. (2001) study, of the 61 women with an eating disorder, 85.2% reported wanting treatment, 57% reported making contact with health services at some time, but only 8% had ever received treatment specifically for their eating disorder. Interestingly, the Hay et al. (1998) study, which recruited 26 women with eating disorders through a general practice, reported that despite an established relationship with a health professional, none of the participants had received a diagnosis for their disorder. (Hart et al., 2011)
I asked above who and how many will benefit from (let’s assumed fulfilled promise of) personalised, more effective treatment based on genetic findings. Presumably, a portion of the 8% that has adequate insurance coverage to qualify for the treatment?
Over coffee last year (Twitter selfie evidence here), Zeynep Yilmaz made the case that these issues are not mutually exclusive: we can focus on putting current knowledge into practice and researching the genetics of eating disorders. In principle, I agree, but I think we must prioritize.
I would argue that we should first focus on utilizing the knowledge we have already generated from decades of research, as opposed to arguing that we need even more research in order to improve outcomes. If we haven’t put into practice what we’ve already established can help (e.g., early intervention), and if we haven’t resolved the issues we know exist (e.g., access to treatment), how can we argue that even more research is needed before outcomes are improved?
Another counter argument is that even among those who do have access to treatment and receive it early, outcomes are poor. According to a review by Steinhausen (2002), among surviving patients (from 119 studies covering 5,590 patients with anorexia nervosa) “less than one-half recovered on average, whereas one-third improved, and 20% remained chronically ill.” It is plausible that understanding the genetic underpinnings of eating disorders may improve outcomes for these patients by identifying genes variants that will enable us to predict which treatment may be more successful, as just one example.
But this is all quite far away, and I would argue that we should be focusing first on putting into practice what we already know will likely help improve outcomes and resolving issues we already know exist by providing timely access to affordable and comprehensive services that already exist at least in some capacity. Perhaps once we do that, we may find that we don’t really need to understand the nitty-gritty biology.
We should think about what we are not focusing on when we focus on hunting gene variants that may be risk factors for eating disorder development or predict treatment success.
I worry that emphasizing the need to understand the genetic basis of eating disorders will lead to disillusionment once study results lead to few, if any, improvements.
I doubt findings from genetic studies will revolutionize eating disorder treatment, and so I worry that hyping up the research will inevitably lead to disappointment.
Recall the ALS Ice Bucket Challenge: $1 million of the funds raised went to a study that identified a gene that contributed to the disease in 3% of cases (news report; actual study). I was actually surprised when I saw that: 3% was much higher than I predicted, and the finding was based on data from only 1,0022 cases.
But ALS is a neurodegenerative disease with a distinct pathology. It is also 100% fatal. There are no successful treatments. The same is not true for eating disorders, where many more factors contribute to onset, maintenance, and illness course.
Here’s just one example of why I am worried we are overpromising: In a paper summarizing the contribution of genome-wise association studies to psychiatry, Ann Collins and Patrick Sullivan (2013) wrote,
For major depressive disorder, a large GWAS [genome-wise association study] mega-analysis (approximately 19 000 participants) failed to identify findings of genome-wide significance. In context, nearly all GWAS with sample sizes above 11 000 participants identified at least one genome-wide significant finding.
This does not mean major depressive disorder does not have genetic components. It may mean that we are not good enough at identifying those components yet because our analysis tools are limited and/or it may mean that there are so many different gene variants and combinations of gene variants that predispose individuals to develop major depressive disorder that they get lost in the wash.
Of course this also does not mean we will never identify genomic regions that confer risk for major depression (or for eating disorders). Basic science research is slow; this is not an argument against it. For eating disorders, it is even slower because of lower prevalence rates. However, if alternatives exist for improving the suffering of individuals today that are not being implemented, is it not irresponsible to argue that we need more basic science research to improve outcomes?
Above, I also wondered: “Will genetic research into eating disorders tell us something we don’t know that we can use in order to improve outcomes or will it just confirm what we already know or what we can ascertain through less expensive, less complex means?”
In summarizing the latest genetic findings in eating disorders, Bulik, Kleiman, and Yilmaz (2016) write,
The co-occurrence of eating disorders and other psychiatric conditions, as well as suicide, is in part due to shared genetic factors.
This is neither surprising nor, I think, very useful. They also write,
Researchers also observed a significant correlation between anorexia nervosa duration of illness and methylation levels [methylation alters the extent to which genes are turned “on/off”, usually turning genes “off”] at probes for genes related to the immune system, liver function, and metabolism, as well as gene pathways associated with anxiety, social functioning, bowel dysfunction, immune function, and liver damage – symptoms commonly reported in patients with anorexia nervosa. … The results of this pilot study suggest that anorexia nervosa – especially if enduring or with early onset – could significantly alter the expression of genes associated with various metabolic, physical, and psychological functions, disruptions in which are some of the key medical and psychiatric complications of anorexia nervosa.
While the finding that there’s a correlation between illness duration and methylation is interesting, I fail to see how this is really telling us anything new. We know that illness duration is negatively predictive of outcome. We know that the longer individuals are ill, the more medical and psychiatric complications they will experience. It is not surprising that these complications are associated with gene expression changes.
There are cooler findings. In 2014, Scott-Van Zeeland et al. reported on associations between an estrogen receptor 2 (EPHX2) and epoxidate hydrolase 2 in anorexia nervosa. A previous study (Wang et al., 2011) has also observed associations between variants of these genes and anorexia nervosa. Bulik et al. write:
EPHX2 was shown to be associated with depression and anxiety in a subgroup of anorexia nervosa cases, as well as BMI and elevated cholesterol in a large longitudinal population cohort.
Another impressive study by Cui and colleagues (2013; open access), using linkage analysis (not the same as a genome-wide association study) and whole genome sequencing, identified two mutations in two different families that are associated with anorexia nervosa or bulimia nervosa. The authors conclude that mutations in one of the genes, which result in decreased activity of that gene, increase the risk of developing an eating disorder.
From a news article:
Typically, research has focused on studying a large number of people to find small genetic variants that may contribute to the risk of developing an eating disorder. But scientists from the University of Iowa and the University of Texas Southwestern Medical Center took the opposite approach: they studied single families in which eating disorders were common across generations. They found that people with mutations in two different genes – ESRRA and HDAC4 – had a 90 percent and 85 percent chance of developing an eating disorder, respectively.
The not-quite-dead scientist in me was excited when reading the original article. This is cool finding, and as Iggy Brady said on Twitter, it is legitimately hypothesis generating. I agree. But the socially-conscious-and-political patient in me was not excited.
“Probably the most useful thing is that it will allow us to study the neurobiology, the underlying cause of eating disorders, and try to find new ways to boost the pathway to prevent them,” says Michael Lutter, an assistant professor of psychiatry at the University of Iowa and the senior author of the study.
Will we be screening everyone for gene variants that increase the risk of eating disorders? Will we develop drugs to boost these pathways and give them to people who have these gene variants? When and, crucially, who will have access to this?
And so this is when things get personal. When I stop getting so excited about the genetics and start thinking about the day-to-day reality of people struggling with eating disorders today. When I start thinking: How we can best improve outcomes today, tomorrow, a year from now, or five years from now — not decades or several decades from now.
Do we need genetics and neurobiology studies to identify new pathways to improve eating disorder outcomes or should we first focus on some easier, faster, and lower-cost strategies?
These strategies are not that hard to conjure if you read the news:
Where is the help for Canadians with eating disorders? (Canada, 2014)
Fears grow as wait lists for eating disorder treatments lengthen (Canada, 2014):
Rostron came back to the hospital where she was first treated – but was faced with a months-long wait. Unwilling and unable to wait, Rostron turned to what she says was the only remaining option – private treatment. “To this point, it’s cost my parents $30,000 and counting. So, it’s very hard,” she said.
At the country’s largest in-patient program at Toronto General Hospital, the wait is three to four months long, for a woman five feet five inches tall and weighing only 60 pounds. Advocates say the wait elsewhere can be up to a year.
Waiting in crisis (Australia, 2013):
… What’s more scary is how hard it is for people with eating disorders in Australia to find help. For instance, in New South Wales there are only five public beds dedicated to eating disorder treatment. Three of those beds are only available to patients in the Westmead catchment area. The other two are located at the Royal Prince Alfred Hospital. This is for the entire state; patients from rural NSW often need to travel to Sydney in order to receive treatment. The waiting lists for these beds can be months long.
For those lucky enough to have private health insurance, the situation is still fraught. In NSW there are only two private hospitals with eating disorder treatment programmes, both with a 4 to 12 week waiting list.
Losing even more weight to get priority treatment for anorexia (Australia, 2016):
Margot placed herself on a waiting list for a bed at a hospital in Sydney. She told Hackthat the hospital said she would have to wait nine months for a place on the inpatient program because she wasn’t in a “critical condition”.
Knowing that in nine months time she may have fallen back into her eating disorder, and may not want to get help anymore, she did something drastic.
She intentionally lost weight to put herself in a critical condition and be moved up the waiting list.
The lives of people seriously ill with eating disorders are being put at risk because they have to wait up to three years for NHS treatment.
Despite widespread awareness of eating disorders, only about a third of those with anorexia nervosa (AN) and only 6% with bulimia nervosa (BN) receive mental health care (NEDA Statistics). For those who do manage to get treatment, the cost ranges from $500 to $2,000 per hospital day in the US. A month of inpatient treatment can easily reach $30,000. The cost of treatment, including therapy and medical monitoring, can extend to $100,000 or more (NEDA).
So, the promises made by genetics researchers — when will they materialize and for whom?
If I were convinced that genetic research is the only or one of the ways to improve outcomes, as it likely is for a disease like ALS, I wouldn’t be writing this. But people have and continue to recover from eating disorders without understanding the genetic underpinnings.
Yes, for the significant percentage of individuals who don’t recover, particularly for individuals where the genetic contributions might be particularly high, understanding the genetic underpinnings may be important, if not crucial.
My fear, however, is that this hunt for gene variants — and the narrative that this is vital for improving outcomes or preventing eating disorders — takes us away from more fruitful battles.
In Part II, I will talk about my concerns regarding the increasingly biomedical framing of eating disorders in the context of neoliberalism and mental health treatment.