What can we learn from the tortuous path to widespread clinical approval of the use of TMS therapy for depression?

Doing TMS circa 2002

The development of transcranial magnetic stimulation (TMS) as a therapy for patients with a depression, has been one of the most important fundamental advances in psychiatric therapeutics since the 1960’s. This is not just hyperbole. Almost all of the drugs we use in psychiatry today are derivative of approaches developed in the 1950s and 1960s. Psychotherapy has certainly improved and evolved but again, the forms used today are direct descendants of approaches developed decades ago. Finally, ECT certainly has improved but remains fundamentally connected to its past. TMS, in contrast, is one of the few essentially new treatments that have developed de novo, and one already helping many thousands of patient.

TMS is really not new, but is only making headway as a treatment in many places around the world now, and only slowly. In fact, the time it has taken for TMS to develop as a treatment has really been quite considerable. The first TMS machine was developed in 1985 but we can’t really date therapeutic TMS from this time as that device could not provide the repetitive stimulation need for treatment applications. Machines that could, however, were developed within the following decade and the first meaningful trials of TMS in depression were published in 1995. It took 13 years until a TMS machine was first approved by the FDA in the US but it is has taken many more years than this, in the majority of cases well over another decade, for approval and widespread uptake to occur in most other countries. This is still not universal.

So given the clear value of TMS, and the inferred premise that it would be better for uptake to have been more widespread, and much more rapid, what can we learn from this experience? In particular, given the increasing proliferation of other brain stimulation techniques, are there lessons that can inform how we address the development of these?

First, it is worth considering the clinical trials that were conducted to evaluate the efficacy of TMS, and those that have been used to test other techniques such as transcranial direct current stimulation (tDCS). In both of these cases, the vast majority of studies have been single site investigator initiated trials with relatively small sample sizes. These type of studies can have value. When a treatment is quite new, smaller studies are appropriate to establish proof of concept. This will be the approach often adopted in phase IIa pharmaceutical trials: get a reasonable indication that there is a therapeutic effect and some indication of the characteristics of the treatment (like an indicative dose range).

However, in the pharmaceutical industry, where there are strong incentives to progress drug development as quickly as possible, positive indications in phase II will usually lead quite directly to substantial phase III trials. This direct progression was mimicked far less  effectively in the TMS case. Although an industry sponsored trial was conducted in the mid 2000’s, and a multi-site NIH sponsored trial followed on from this, this all occurred after the conduct of a really diverse array of small, mostly underpowered trials. These trials ultimately contributed very little to the clinical progression of the treatment.

Now clearly the commercial status of TMS played a large role in this story. The conduct of the Neuronetics registration trial in the mid 2000’s, and the Brainsway registration trial of deep TMS that followed later, were only possible because these companies had unique intellectual property related to their TMS coils: these provided for the possibility of some temporary market monopoly motivating the considerable investment (tens of millions of dollars) spent to conduct these trials. In contrast, the first companies selling TMS machines did not have the intellectual property protection or financial wherewithal to sponsor major research endeavours.

These financial factors have influenced every aspect of the spread and uptake of TMS since that time.  Outside the US market, there has been very limited commercial sponsorship of regulatory applications and few attempts by industry to systematically collect additional clinical trial or health economic data that might be needed for regulatory or funding approval in smaller or more fragmented markets.

The situation in Australia is a good case in point. Registration of medical devices with the Therapeutics Goods Administration (TGA) to allow clinical use in Australia is relatively uncomplicated using a system harmonized with the EU. Therefore, multiple TMS devices have progressively been listed for clinical use. However, regulatory listing does not link to public funding, and outside the provision of TMS to inpatients in private psychiatric hospitals – a uniquely Australian and lucrative activity for these hospitals – widespread adoption of outpatient TMS has not occurred yet in Australia, over 20 years after the first trials were conducted in the country. Funding for outpatient TMS can only come through the public funding agency Medicare (private insurers cannot fund outpatient procedures like TMS). However, there has been no attempt by the TMS device manufacturers to initiate and carry forward a funding application. Neuronetics flirted with the idea of doing this for some time but ultimately chose not to and the lack of monopoly status, and the relatively small scale of the other manufacturers presumably prevented them from taking on this task.

It was ultimately left to a series of individual psychiatrists to attempt this, under the distant and uninvolved mandate of the Royal Australian and New Zealand College of Psychiatrists. It is worthy of note that the college refused to provide any practical financial or professional support to these applications, the last of which has passed the committee review considered the most critical step to achieve funding. A number of applications were filed over time: I was responsible for the last three in a process spanning seven years.
From this experience I can confidently say the delay in achieving approval was directly related to the lack of professional, experienced support. This is not a job to be taken on by busy clinicians or researchers with any expectation of success. As an aside, our success only really became possible when I persuaded a group of TMS device manufactures and distributors to contribute relatively limited amounts each to help pay for the services of a professional agency to help in the process of preparation of our applications. Without this, I do not think we would have had any chance of success. In contrast, a professionally authored application may well have had success quite some time ago, making TMS therapy accessible to patients years earlier.

The stop start process we engaged in, learning a lot but taking a long time, is quite different from that which would be taken by a company of meaningful size applying for regulatory approval of a drug or device. Established companies have experienced regulatory teams with the health economic expertise often required to support these applications and they would not expect a process like this to take seven years, or over a decade.

It is also notable that uptake internationally of TMS has been highly varied. In part this has related to the location in certain countries of TMS research expertise: hubs around which clinical programs and training  can develop. Early adoption of new therapies often develops out centers of research excellence. However, it is more influenced by the regulatory factors we have been discussing and whether there is the capacity of industry, or clinical groups, to navigate the regulations on a country by country basis.
It is also true that the evidence required by regulatory agencies differs significantly between countries. Companies are motivated to conduct traditional sham controlled trials as these are typically required by the FDA in gain access to the lucrative US market. In Australia, however, the Medicare Services Advisory Committee evaluates new therapies based on where a new treatment is proposed to fit into a defined clinical protocol. They are most interested in trials evaluating efficacy compared to the existing standard of care, not sham or placebo treatment. This greatly limits the applicability of data collected for US approval to the Australian assessment process.

So what can we learn from this? To more effectively progress the development of new brain stimulation therapies, or other novel treatments, especially those without strong industry support? I think the main thing we can do, when developing and testing new treatment approaches, is to organize and collaborate more.  Groups getting together to conduct multi-site trials have much more capacity to progress the field than researchers or groups conducting smaller studies in isolation. Collaboration means compromise. Not everyone will have their ‘special’ protocol tested: trials need to be developed by consensus. However, doing a small study of your special protocol is probably not going to advance it all that much anyway.

Collaborative studies are complex to get funded and to conduct.  This is especially challenging if we are reaching across national boundaries. However, grant agencies are increasingly interested in international collaboration (and hopefully this will survive COVID!). Researchers have to accept that being a mid level author on an outstanding paper describing a large successful collaborative trial is as good, if not better than, being first author on a much less prestigious publication. Some areas have done this extremely well. Clinical trials performed by intensive care researchers in Australia are routinely published in the very best journals as they are conducted regularly by a highly functional national clinical trials network. They get great publications, but more importantly, regularly impact clinical practice as they are large and substantive trials. We also need to learn to judge our colleagues track records, when they apply for grants or promotion, to take this into account.

I think we can also usefully adopt a more commercially oriented mindset when conducting clinical trials, even when these are investigator initiated and not connected to industry anyway. Is the trial being proposed explicitly a proof of concept study and if concept has been established, should we not progress quite rapidly to something definitive?

The approval of ‘theta burst’ TMS for use in depression by the FDA in the US in recent years has established a really meaningful precedent. This approval came from a clinical trial that was exclusively conducted by independent researchers without any industry involvement. It should inspire the field to think about how studies we conduct can be developed in a way that can be used in regulatory applications as in reality this is the most direct pathway towards widespread clinical use. This might involve thinking about the actual design of specific trials or the collection of data that can support health economic evaluations. It certainly will always involve consideration of the size and scope of the proposed research.
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We should also think about whether we can develop new models of engagement between academic groups and companies in the brain stimulation area. Many brain stimulation device manufacturers are quite small and have either struggled to, or chosen not to, invest the substantial money required to conduct registration scale clinical trials. If promising intellectual property is held by a company that does not have the capacity to conduct the clinical trials to advance a specific application, having these studies done by a publicly funded research group might seem quite unreasonable to some if the commercial benefit of the outcomes of this research are exclusively captured in the future by the company in question. Perhaps there is a way in which future commercial earnings related to this research can somehow be shared with the researchers who have done the critical work to develop the approach or even the agency responsible for funding it. This type of idea would require a fundamental reconsideration of the relationships between government funded research, university or hospital research centers and industry but certainly warrants consideration and thought.

In summary, the clinical development of forms of non invasive brain stimulation has so far been inefficient: too slow and fragmented to provide patients with access to new treatments, especially TMS, in a timely manner that reflects the seriousness of their illnesses.  Researchers need to think carefully in the design and implementation of new studies: we need to learn from our successes and our failures. We need to be both creative and determined and to be constantly aware of the pressing clinical needs that motivate the development of novel therapeutics for disorders affecting mental health.