Questionable Enrollment Math at the UK's NIHR

There has been considerable noise coming out of the UK lately about successes in clinical trial enrollment.

First, a couple months ago came the rather dramatic announcement that clinical trial participation in the UK had "tripled over the last 6 years". That announcement, by the chief executive of the

Sweet creature of bombast: is Sir John
writing press releases for the NIHR?

National Institute of Health Research's Clinical Research Network, was quickly and uncritically picked up by the media.

That immediately caught my attention. In large, global trials, most pharmaceutical companies I've worked with can do a reasonable job of predicting accrual levels in a given country. I like to think that if participation rates in any given country had jumped that heavily, I’d have heard something.

(To give an example: looking at a quite-typical study I worked on a few years ago: UK sites were overall slightly below the global average. The highest-enrolling countries were about 2.5 times as fast. So, a 3-fold increase in accruals would have catapulted the UK from below average to the fastest-enrolling country in the world.)

Further inquiry, however, failed to turn up any evidence that the reported tripling actually corresponded to more human beings enrolled in clinical trials. Instead, there is some reason to believe that all we witnessed was increased reporting of trial participation numbers.

Now we have a new source of wonder, and a new giant multiplier coming out of the UK. As the Director of the NIHR's Mental Health Research Network, Til Wykes, put it in her blog coverage of her own paper:

Our research on the largest database of UK mental health studies shows that involving just one or two patients in the study team means studies are 4 times more likely to recruit successfully.

Again, amazing! And not just a tripling – a quadrupling!

Understand: I spend a lot of my time trying to convince study teams to take a more patient-focused approach to clinical trial design and execution. I desperately want to believe this study, and I would love having hard evidence to bring to my clients.

At first glance, the data set seems robust. From the King's College press release:

Published in the British Journal of Psychiatry, the researchers analysed 374 studies registered with the Mental Health Research Network (MHRN).

Studies which included collaboration with service users in designing or running the trial were 1.63 times more likely to recruit to target than studies which only consulted service users.  Studies which involved more partnerships - a higher level of Patient and Public Involvement (PPI) - were 4.12 times more likely to recruit to target.

But here the first crack appears. It's clear from the paper that the analysis of recruitment success was not based on 374 studies, but rather a much smaller subset of 124 studies. That's not mentioned in either of the above-linked articles.

And at this point, we have to stop, set aside our enthusiasm, and read the full paper. And at this point, critical doubts begin to spring up, pretty much everywhere.

First and foremost: I don’t know any nice way to say this, but the "4 times more likely" line is, quite clearly, a fiction. What is reported in the paper is a 4.12 odds ratio between "low involvement" studies and "high involvement" studies (more on those terms in just a bit).  Odds ratios are often used in reporting differences between groups, but they are unequivocally not the same as "times more likely than".

This is not a technical statistical quibble. The authors unfortunately don’t provide the actual success rates for different kinds of studies, but here is a quick example that, given other data they present, is probably reasonably close:

• A Studies: 16 successful out of 20 
• Probability of success: 80% 
• Odds of success: 4 to 1
• B Studies: 40 successful out of 80
• Probability of success: 50%
• Odds of success: 1 to 1

From the above, it’s reasonable to conclude that A studies are 60% more likely to be successful than B studies (the A studies are 1.6 times as likely to succeed). However, the odds ratio is 4.0, similar to the difference in the paper. It makes no sense to say that A studies are 4 times more likely to succeed than B studies.

This is elementary stuff. I’m confident that everyone involved in the conduct and analysis of the MHRN paper knows this already. So why would Dr Wykes write this? I don’t know; it's baffling. Maybe someone with more knowledge of the politics of British medicine can enlighten me.

If a pharmaceutical company had promoted a drug with this math, the warning letters and fines would be flying in the door fast. And rightly so. But if a government leader says it, it just gets recycled verbatim.

The other part of Dr Wykes's statement is almost equally confusing. She claims that the enrollment benefit occurs when "involving just one or two patients in the study team". However, involving one or two patients would seem to correspond to either the lowest ("patient consultation") or the middle level of reported patient involvement (“researcher initiated collaboration”). In fact, the "high involvement" categories that are supposed to be associated with enrollment success are studies that were either fully designed by patients, or were initiated by patients and researchers equally. So, if there is truly a causal relationship at work here, improving enrollment would not be merely a function of adding a patient or two to the conversation.

There are a number of other frustrating aspects of this study as well. It doesn't actually measure patient involvement in any specific research program, but uses just 3 broad categories (that the researchers specified at the beginning of each study). It uses an arbitrary and undocumented 17-point scale to measure "study complexity", which collapses and quite likely underweights many critical factors into a single number. The enrollment analysis excluded 11 studies because they weren't adequate for a factor that was later deemed non-significant. And probably the most frustrating facet of the paper is that the authors share absolutely no descriptive data about the studies involved in the enrollment analysis. It would be completely impossible to attempt to replicate its methods or verify its analysis. Do the authors believe that "Public Involvement" is only good when it’s not focused on their own work?

However, my feelings about the study and paper are an insignificant fraction of the frustration I feel about the public portrayal of the data by people who should clearly know better. After all, limited evidence is still evidence, and every study can add something to our knowledge. But the public misrepresentation of the evidence by leaders in the area can only do us harm: it has the potential to actively distort research priorities and funding.

Why This Matters

We all seem to agree that research is too slow. Low clinical trial enrollment wastes time, money, and the health of patients who need better treatment options.

However, what's also clear is that we lack reliable evidence on what activities enable us to accelerate the pace of enrollment without sacrificing quality. If we are serious about improving clinical trial accrual, we owe it to our patients to demand robust evidence for what works and what doesn’t. Relying on weak evidence that we've already solved the problem ("we've tripled enrollment!") or have a method to magically solve it ("PPI quadrupled enrollment!") will cause us to divert significant time, energy, and human health into areas that are politically favored but less than certain to produce benefit. And the overhyping those results by research leadership compounds that problem substantially. NIHR leadership should reconsider its approach to public discussion of its research, and practice what it preaches: critical assessment of the data.

[Update Sept. 20: The authors of the study have posted a lengthy comment below. My follow-up is here.]
 
[Image via flikr user Elliot Brown.]

Ennis L, & Wykes T (2013). Impact of patient involvement in mental health research: longitudinal study. The British journal of psychiatry : the journal of mental science PMID: 24029538

Every Unhappy PREA Study is Unhappy in its Own Way

“Children are not small adults.” We invoke this saying, in a vague and hand-wavy manner, whenever we talk about the need to study drugs in pediatric populations. It’s an interesting idea, but it really cries out for further elaboration. If they’re not small adults, what are they? Are pediatric efficacy and safety totally uncorrelated with adult efficacy and safety? Or are children actually kind of like small adults in certain important ways?

Pediatric post-marketing studies have been completed for over 200 compounds in the years since BPCA (2002, offering a reward of 6 months extra market exclusivity/patent life to any drug conducting requested pediatric studies) and PREA (2007, giving FDA power to require pediatric studies) were enacted. I think it is fair to say that at this point, it would be nice to have some sort of comprehensive idea of how FDA views the risks associated with treating children with medications tested only on adults. Are they in general less efficacious? More? Is PK in children predictable from adult studies a reasonable percentage of the time, or does it need to be recharacterized with every drug?

Essentially, my point is that BPCA/PREA is a pretty crude tool: it is both too broad in setting what is basically a single standard for all new adult medications, and too vague as to what exactly that standard is.

In fact, a 2008 published review from FDA staffers and a 2012 Institute of Medicine report both show one clear trend: in a significant majority of cases, pediatric studies resulted in validating the adult medication in children, mostly with predictable dose and formulation adjustments (77 of 108 compounds (71%) in the FDA review, and 27 of 45 (60%) in the IOM review, had label changes that simply reflected that use of the drug was acceptable in younger patients).

So, it seems, most of the time, children are in fact not terribly unlike small adults.

But it’s also true that the percentages of studies that show lack of efficacy, or bring to light a new safety issue with the drug’s use in children, is well above zero. There is some extremely important information here.

To paraphrase John Wanamaker: we know that half our PREA studies are a waste of time; we just don’t know which half.

This would seem to me to be the highest regulatory priority – to be able to predict which new drugs will work as expected in children, and which may truly require further study. After a couple hundred compounds have gone through this process, we really ought to be better positioned to understand how certain pharmacological properties might increase or decrease the risks of drugs behaving differently than expected in children. Unfortunately, neither the FDA nor the IOM papers venture any hypotheses about this – both end up providing long lists of examples of certain points, but not providing any explanatory mechanisms that might enable us to engage in some predictive risk assessment.

While FDASIA did not advance PREA in terms of more rigorously defining the scope of pediatric requirements (or, better yet, requiring FDA to do so), it did address one lingering concern by requiring that FDA publish non-compliance letters for sponsors that do not meet their commitments. (PREA, like FDAAA, is a bit plagued by lingering suspicions that it’s widely ignored by industry.)

The first batch of letters and responses has been published, and it offers some early insights into the problems engendered by the nebulous nature of PREA and its implementation.

These examples, unfortunately, are still a bit opaque – we will need to wait on the FDA responses to the sponsors to see if some of the counter-claims are deemed credible. In addition, there are a few references to prior deferral requests, but the details of the request (and rationales for the subsequent FDA denials) do not appear to be publicly available. You can read FDA’s take on the new postings on their blog, or in the predictably excellent coverage from Alec Gaffney at RAPS.

Looking through the first 4 drugs publicly identified for noncompliance, the clear trend is that there is no trend. All these PREA requirements have been missed for dramatically different reasons.

Here’s a quick rundown of the drugs at issue – and, more interestingly, the sponsor responses:

1. Renvela - Genzyme (full response)

Genzyme appears to be laying responsibility for the delay firmly at FDA’s feet here, basically claiming that FDA continued to pile on new requirements over time:

Genzyme’s correspondence with the FDA regarding pediatric plans and design of this study began in 2006 and included a face to face meeting with FDA in May 2009. Genzyme submitted 8 revisions of the pediatric study design based on feedback from FDA including that received in 4 General Advice Letters. The Advice Letter dated February 17, 2011  contained further recommendations on the study design, yet still required the final clinical study report  by December 31, 2011.

This highlights one of PREA’s real problems: the requirements as specified in most drug approval letters are not specific enough to fully dictate the study protocol. Instead, there is a lot of back and forth between the sponsor and FDA, and it seems that FDA does not always fully account for their own contribution to delays in getting studies started.

2. Hectorol - Genzyme (full response)

In this one, Genzyme blames the FDA not for too much feedback, but for none at all:

On December 22, 2010, Genzyme submitted a revised pediatric development plan (Serial No. 212) which was intended to address FDA feedback and concerns that had been received to date. This submission included proposed protocol HECT05310. [...] At this time, Genzyme has not received feedback from the FDA on the protocol included in the December 22, 2010 submission.

If this is true, it appears extremely embarrassing for FDA. Have they really not provided feedback in over 2.5 years, and yet still sending noncompliance letters to the sponsor? It will be very interesting to see an FDA response to this.

3. Cleviprex – The Medicines Company (full response)

This is the only case where the pharma company appears to be clearly trying to game the system a bit. According to their response:

Recognizing that, due to circumstances beyond the company’s control, the pediatric assessment could not be completed by the due date, The Medicines Company notified FDA in September 2010, and sought an extension. At that time, it was FDA’s view that no extensions were available. Following the passage of FDASIA, which specifically authorizes deferral extensions, the company again sought a deferral extension in December 2012. 

So, after hearing that they had to move forward in 2010, the company promptly waited 2 years to ask for another extension. During that time, the letter seems to imply that they did not try to move the study forward at all, preferring to roll the dice and wait for changing laws to help them get out from under the obligation.

4. Twinject/Adrenaclick – Amedra (full response)

The details of this one are heavily redacted, but it may also be a bit of gamesmanship from the sponsor. After purchasing the injectors, Amedra asked for a deferral. When the deferral was denied, they simply asked for the requirements to be waived altogether. That seems backwards, but perhaps there's a good reason for that.

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Clearly, 4 drugs is not a sufficient sample to say anything definitive, especially when we don't have FDA's take on the sponsor responses. However, it is interesting that these 4 cases seem to reflect an overall pattern with BCPA and PREA - results are scattershot and anecdotal. We could all clearly benefit from a more systematic assessment of why these trials work and why some of them don't, with a goal of someday soon abandoning one-size-fits-all regulation and focusing resources where they will do the most good.

Counterfeit Drugs in Clinical Trials?

This morning I ran across a bit of a coffee-spitter: in the middle of an otherwise opaquely underinformative press release fromTranscelerate Biopharma about the launch of their

Counterfeits flooding
the market? Really?

"Comparator Network" - which will perhaps streamline member companies' ability to obtain drugs from each other for clinical trials using active comparator arms -  the CEO of the consortium, Dalvir Gill, drops a rather remarkable quote:

"Locating and accessing these comparators at the right time, in the right quantities and with the accompanying drug stability and regulatory information we need, doesn't always happen efficiently. This is further complicated by infiltration of the commercial drug supply chain by counterfeit drugs.  With the activation of our Comparator Network the participating TransCelerate companies will be able to source these comparator drugs directly from each other, be able to secure supply when they need it in the quantities they need, have access to drug data and totally mitigate the risk of counterfeit drugs in that clinical trial."

[Emphasis added.]

I have to admit to being a little floored by the idea that there is any sort of risk, in industry-run clinical trials, of counterfeit medication "infiltration".

Does Gill know something that the rest of us don't? Or is this just an awkward slap at perceived competition – innuendo against the companies that currently manage clinical trial comparator drug supply? Or an attempt at depicting the trials of non-Transcelerate members as risky and prone to fraud?

Either way, it could use some explaining. Thinking I might have missed something, I did do a quick literature search to see if I could come across any references to counterfeits in trials. Google Scholar and PubMed produced no useful results, but Wikipedia helpfully noted in its entry on counterfeit medications:

Counterfeit drugs have even been known to have been involved in clinical drug trials.^{[citation needed]}

And on that point, I think we can agree: Citation needed. I hope the folks at Transcelerate will oblige.