Clinical Trial Enrollment, ASCO 2013 Edition

Even by the already-painfully-embarrassingly-low standards of clinical trial enrollment in general, patient enrollment in cancer clinical trials is slow. Horribly slow. In many cancer trials, randomizing one patient every three or four months isn't bad at all – in fact, it's par for the course. The most
commonly-cited number is that only 3% of cancer patients participate in a trial – and although exact details of how that number is measured are remarkably difficult to pin down, it certainly can't be too far from reality.

Ultimately, the cost of slow enrollment is borne almost entirely by patients; their payment takes the form of fewer new therapies and less evidence to support their treatment decisions.

So when a couple dozen thousand of the world's top oncologists fly into Chicago to meet, you'd figure that improving accrual would be high on everyone’s agenda. You can't run your trial without patients, after all.

But every year, the annual ASCO meeting underdelivers in new ideas for getting more patients into trials. I suppose this a consequence of ASCO's members-only focus: getting the oncologists themselves to address patient accrual is a bit like asking NASCAR drivers to tackle the problems of aerodynamics, engine design, and fuel chemistry.

Nonetheless, every year, a few brave souls do try. Here is a quick rundown of accrual-related abstracts at this year’s meeting, conveniently sorted into 3 logical categories:

1. As Lord Kelvin may or may not have said, “If you cannot measure it, you cannot improve it.”

• Abstract e15572: Inadequate data availability on clinical trial accrual and its effect on progress in cancer research

Probably the most sensible of this year's crop, because rather than trying to make something out of nothing, the authors measure exactly how pervasive the nothing is. Specifically, they attempt to obtain fairly basic patient accrual data for the last three years' worth of clinical trials in kidney cancer. Out of 108 trials identified, they managed to get – via search and direct inquiries with the trial sponsors – basic accrual data for only 43 (40%).

That certainly qualifies as “terrible”, though the authors content themselves with “poor”.

Interestingly, exactly zero of the 32 industry-sponsored trials responded to the authors' initial survey. This fits with my impression that pharma companies continue to think of accrual data as proprietary, though what sort of business advantage it gives them is unclear. Any one company will have only run a small fraction of these studies, greatly limiting their ability to draw anything resembling a valid conclusion.

• Abstract TPS6645: Predictors of accrual success for cooperative group trials: The Cancer and Leukemia Group B (Alliance) experience

CALGB investigators look at 110 trials over the past 10 years to see if they can identify any predictive markers of successful enrollment. Unfortunately, the trials themselves are pretty heterogeneous (accrual periods ranged from 6 months to 8.8 years), so finding a consistent marker for successful trials would seem unlikely.

And, in fact, none of the usual suspects (e.g., startup time, disease prevalence) appears to have been significant. The exception was provision of medication by the study, which was positively associated with successful enrollment.

The major limitation with this study, apart from the variability of trials measured, is in its definition of “successful”, which is simply the total number of planned enrolled patients. Under both of their definitions, a slow-enrolling trial that drags on for years before finally reaching its goal is successful, whereas if that same trial had been stopped early it is counted as unsuccessful. While that sometimes may be the case, it's easy to imagine situations where allowing a slow trial to drag on is a painful waste of resources – especially if results are delayed enough to bring their relevance into question.

Even worse, though, is that a trial’s enrollment goal is itself a prediction. The trial steering committee determines how many sites, and what resources, will be needed to hit the number needed for analysis. So in the end, this study is attempting to identify predictors of successful predictions, and there is no reason to believe that the initial enrollment predictions were made with any consistent methodology.

2. If you don't know, maybe ask somebody?

• Abstract 8592: Strategies to overcome barriers to accrual (BtA) to NCI-sponsored clinical trials: A project of the NCI-Myeloma Steering Committee Accrual Working Group (NCI-MYSC AWG)
  
• Abstract 1596: Rapid online feedback to improve clinical trial accrual: CODEL anaplastic glioma (AG) (NCCTG/Alliance N0577) as a model

With these two abstracts we celebrate and continue the time-honored tradition of alchemy, whereby we transmute base opinion into golden data. The magic number appears to be 100: if you've got 3 digits' worth of doctors telling you how they feel, that must be worth something.

In the first abstract, a working group is formed to identify and vote on the major barriers to accrual in oncology trials. Then – and this is where the magic happens – that same group is asked to identify and vote on possible ways to overcome those barriers.

In the second, a diverse assortment of community oncologists were given an online survey to provide feedback on the design of a phase 3 trial in light of recent new data. The abstract doesn't specify who was initially sent the survey, so we cannot tell response rate, or compare survey responders to the general population (I'll take a wild guess and go with “massive response bias”).

Market research is sometimes useful. But what cancer clinical trial do not need right now are more surveys are working groups. The “strategies” listed in the first abstract are part of the same cluster of ideas that have been on the table for years now, with no appreciable increase in trial accrual.

3. The obligatory “What the What?” abstract

• Abstract 6564: Minority accrual on a prospective study targeting a diverse U.S. breast cancer population: An analysis of Wake Forest CCOP research base protocol 97609

The force with which my head hit my desk after reading this abstract made me concerned that it had left permanent scarring.

If this had been re-titled “Poor Measurement of Accrual Factors Leads to Inaccurate Accrual Reporting”, would it still have been accepted for this year’s meeting? That's certainly a more accurate title.

Let’s review: a trial intends to enroll both white and minority patients. Whites enroll much faster, leading to a period where only minority patients are recruited. Then, according to the authors, “an almost 4-fold increase in minority accrual raises question of accrual disparity.” So, sites will only recruit minority patients when they have no choice?

But wait: the number of sites wasn't the same during the two periods, and start-up times were staggered. Adjusting for actual site time, the average minority accrual rate was 0.60 patients/site/month in the first part and 0.56 in the second. So the apparent 4-fold increase was entirely an artifact of bad math.

This would be horribly embarrassing were it not for the fact that bad math seems to be endemic in clinical trial enrollment. Failing to adjust for start-up time and number of sites is so routine that not doing it is grounds for a presentation.

The bottom line

What we need now is to rigorously (and prospectively) compare and measure accrual interventions. We have lots of candidate ideas, and there is no need for more retrospective studies, working groups, or opinion polls to speculate on which ones will work best.  Where possible, accrual interventions should themselves be randomized to minimize confounding variables which prevent accurate assessment. Data needs to be uniformly and completely collected. In other words, the standards that we already use for clinical trials need to be applied to the enrollment measures we use to engage patients to participate in those trials.

This is not an optional consideration. It is an ethical obligation we have to cancer patients: we need to assure that we are doing all we can to maximize the rate at which we generate new evidence and test new therapies.

[Image credit: Logarithmic turtle accrual rates courtesy of Flikr user joleson.]

Placebos: Banned in Helsinki?

One of the unintended consequences of my (admittedly, somewhat impulsive) decision to name this blog is that I get a fair bit of traffic from Google: people searching for placebo-related information.

Some recent searches have been about the proposed new revisions to the Declaration of Helsinki, and how the new draft version will prohibit or restrict the use of placebo controls in clinical trials. This was a bit puzzling, given that the publicly-released draft revisions [PDF] didn't appear to substantially change the DoH's placebo section.

Much of the confusion appears to be caused by a couple sources. First, the popular Pharmalot blog (whose approach to critical analysis I've noted before as being ... well ... occasionally unenthusiastic) covered it thus:

The draft, which was released earlier this week, is designed to update a version that was adopted in 2008 and many of the changes focus on the use of placebos. For instance, placebos are only permitted when no proven intervention exists; patients will not be subject to any risk or there must be ‘compelling and sound methodological reasons’ for using a placebo or less effective treatment.

This isn't a good summary of the changes, since the “for instance” items are for the most part slight re-wordings from the 2008 version, which itself didn't change much from the version adopted in 2000.

To see what I mean, take a look at the change-tracked version of the placebo section:

The benefits, risks, burdens and effectiveness of a new intervention must be tested against those of the best current proven intervention(s), except in the following circumstances: 

The use of placebo, or no treatment intervention is acceptable in studies where no current proven intervention exists; or 

Where for compelling and scientifically sound methodological reasons the use of any intervention less effective than the best proven one, placebo or no treatment is necessary to determine the efficacy or safety of an intervention 

and the patients who receive any intervention less effective than the best proven one, placebo or no treatment will not be subject to any additional risks of serious or irreversible harm as a result of not receiving the best proven intervention.  

Extreme care must be taken to avoid abuse of this option.

Really, there is only one significant change to this section: the strengthening of the existing reference to “best proven intervention” in the first sentence. It was already there, but has now been added to sentences 3 and 4. This is a reference to the use of active (non-placebo) comparators that are not the “best proven” intervention.

So, ironically, the biggest change to the placebo section is not about placebos at all.

This is a bit unfortunate, because to me it subtracts from the overall clarity of the section, since it's no longer exclusively about placebo despite still being titled “Use of Placebo”. The DoH has been consistently criticized during previous rounds of revision for becoming progressively less organized and coherently structured, and it certainly reads like a rambling list of semi-related thoughts – a classic “document by committee”. This lack of structure and clarity certainly hurt the DoH's effectiveness in shaping the world's approach to ethical clinical research.

Even worse, the revisions continue to leave unresolved the very real divisions that exist in ethical beliefs about placebo use in trials. The really dramatic revision to the placebo section happened over a decade ago, with the 2000 revision. Those changes, which introduced much of the strict wording in the current version, were extremely controversial, and resulted in the issuance of an extraordinary “Note of Clarification” that effectively softened the new and inflexible language. The 2008 version absorbed the wording from the Note of Clarification, and the resulting document is now vague enough that it is interpreted quite differently in different countries. (For more on the revision history and controversy, see this comprehensive review.)

The 2013 revision could have been an opportunity to try again to build a consensus around placebo use. At the very least, it could have acknowledged and clarified the division of beliefs on the topic. Instead, it sticks to its ambiguous phrasing which will continue to support multiple conflicting interpretations. This does not serve the ends of assuring the ethical conduct of clinical trials.

Ezekiel Emmanuel has been a long-time critic of the DoH's lack of clarity and structure. Earlier this month, he published a compact but forceful review of the ways in which the Declaration has become weakened by its long series of revisions:

Over the years problems with, and objections to, the document have accumulated. I propose that there are nine distinct problems with the current version of the Declaration of Helsinki: it has an incoherent structure; it confuses medical care and research; it addresses the wrong audience; it makes extraneous ethical provisions; it includes contradictions; it contains unnecessary repetitions; it uses multiple and poor phrasings; it includes excessive details; and it makes unjustified, unethical recommendations.

Importantly, Emmanuel also includes a proposed revision and restructuring of the DoH. In his version, much of the current wording around placebo use is retained, but it is absorbed into the larger concept of “Scientific Validity”, which adds important context to the decision about how to decide on a comparator arm in general.

Here is Emmanuel’s suggested revision:

Scientific Validity:  Research in biomedical and other sciences involving human participants must conform to generally accepted scientific principles, be based on a thorough knowledge of the scientific literature, other relevant sources of information, and suitable laboratory, and as necessary, animal experimentation.  Research must be conducted in a manner that will produce reliable and valid data.  To produce meaningful and valid data new interventions should be tested against the best current proven intervention. Sometimes it will be appropriate to test new interventions against placebo, or no treatment, when there is no current proven intervention or, where for compelling and scientifically sound methodological reasons the use of placebo is necessary to determine the efficacy and/or safety of an intervention and the patients who receive placebo, or no treatment, will not be subject to excessive risk or serious irreversible harm.  This option should not be abused.

Here, the scientific rationale for the use of placebo is placed in the greater context of selecting a control arm, which is itself subservient to the ethical imperative to only conduct studies that are scientifically valid. One can quibble with the wording (I still have issues with the use of “best proven” interventions, which I think is much too undefined here, as it is in the DoH, and glosses over some significant problems), but structurally this is a lot stronger, and provides firmer grounding for ethical decision making.

Emanuel, E. (2013). Reconsidering the Declaration of Helsinki The Lancet, 381 (9877), 1532-1533 DOI: 10.1016/S0140-6736(13)60970-8

[Image: Extra-strength chill pill, modified by the author, based on an original image by Flikr user mirjoran.]

The Case against Randomized Trials is, Fittingly, Anecdotal

I have a lot of respect for Eric Topol, and am a huge fan of his ongoing work to bring new mobile technology to benefit patients.

The Trial of the Future

However, I am simply baffled by this short video he recently posted on his Medscape blog. In it, he argues against the continued use of randomized controlled trials (RCTs) to provide evidence for or against new drugs.

His argument for this is two anecdotes: one negative, one positive. The negative anecdote is about the recently approved drug for melanoma, Zelboraf:

Well, that's great if one can do [RCTs], but often we're talking about needing thousands, if not tens of thousands, of patients for these types of clinical trials. And things are changing so fast with respect to medicine and, for example, genomically guided interventions that it's going to become increasingly difficult to justify these very large clinical trials. 

For example, there was a drug trial for melanoma and the mutation of BRAF, which is the gene that is found in about 60% of people with malignant melanoma. When that trial was done, there was a placebo control, and there was a big ethical charge asking whether it is justifiable to have a body count. This was a matched drug for the biology underpinning metastatic melanoma, which is essentially a fatal condition within 1 year, and researchers were giving some individuals a placebo.

First and foremost, this is simply factually incorrect on a couple extremely important points.

1. Zelboraf was not approved based on any placebo-controlled trials. The phase 1 and phase 2 trials were both single-arm, open label studies. The only phase 3 trial run before FDA approval used dacarbazine in the comparator arm. In fact, of the 34 trials currently listed for Zelboraf on ClinicalTrials.gov, only one has a placebo control: it’s an adjuvant trial for patients whose melanoma has been completely resected, where no treatment may very well be the best option.
2. The Zelboraf trials are not an example of “needing thousands, if not tens of thousands, of patients” for approval. The phase 3 trial enrolled 675 patients. Even adding the phase 1 and 2 trials doesn’t get us to 1000 patients.

Correcting these details take a lot away from the power of this single drug to be a good example of why we should stop using “the sanctimonious [sic] randomized, placebo-controlled clinical trial”.

The second anecdote is about a novel Alzheimer’s Disease candidate:

A remarkable example of a trial of the future was announced in May. For this trial, the National Institutes of Health is working with [Banner Alzheimer's Institute] in Arizona, the University of Antioquia in Colombia, and Genentech to have a specific mutation studied in a large extended family living in the country of Colombia in South America. There is a family of 8000 individuals who have the so-called Paisa mutation, a presenilin gene mutation, which results in every member of this family developing dementia in their 40s. 

Researchers will be testing a drug that binds amyloid, a monoclonal antibody, in just 300 family members. They're not following these patients out to the point of where they get dementia. Instead, they are using surrogate markers to see whether or not the process of developing Alzheimer's can be blocked using this drug. This is an exciting way in which we can study treatments that can potentially prevent Alzheimer's in a very well-demarcated, very restricted population with a genetic defect, and then branch out to a much broader population of people who are at risk for Alzheimer's. These are the types of trials of the future. 

There are some additional disturbing factual errors here – the extended family numbers about 5,000, not 8,000. And estimates of the prevalence of the mutation within that family appear to vary from about one-third to one-half, so it’s simply wrong to state that “every member of this family” will develop dementia.

However, those errors are relatively minor, and are completely overshadowed by the massive irony that this is a randomized, placebo-controlled trial. Only 100 of the 300 trial participants will receive the active study drug, crenezumab. The other 200 will be on placebo.

And so, the “trial of the future” held up as a way to get us out of using randomized, placebo-controlled trials is actually a randomized, placebo-controlled trial itself. I hope you can understand why I’m completely baffled that Topol thinks this is evidence of anything.

Finally, I have to ask: how is this the trial of the future, anyway? It is a short-term study on a highly-selected patient population with a specific genetic profile, measuring surrogate markers to provide proof of concept for later, larger studies. Is it just me, or does that sound exactly like the early lovastatin trials of the mid-1980’s, which tested cholesterol reduction in a small population of patients with severe heterozygous familial hypercholesterolemia? Back to the Future, indeed.


[Image: time-travelling supercar courtesy of Flickr user JoshBerglund19.]

Public Protocols? Burying the lede on the TEST Act

Not to be confused with the Test Act.
(via Luminarium)

4 Democratic members of Congress recently co-sponsored the TEST (Trial and Experimental Studies Transparency) Act, which is intended to expand the scope of mandatory registration of clinical trials. Coverage so far has been light, and mainly consists of uncritical recycling of the press release put out by congressman Markey’s office.

Which is unfortunate, because nowhere in that release is there a single mention of the bill’s most controversial feature: publication of clinical trial "supporting documents", including the patient’s Informed Consent Form (ICF) and, incredibly, the entire protocol (including any and all subsequent amendments to the protocol).

How Rep. Markey and colleagues managed to put out a 1,000-word press release without mentioning this detail is nothing short of remarkable. Is the intent to try to sneak this through?

Full public posting of every clinical trial protocol would represent an enormous shift in how R&D is conducted in this country (and, therefore, in the entire world). It would radically alter the dynamics of how pharmaceutical companies operate by ripping out a giant chunk of every company’s proprietary investment – essentially, confiscating and nationalizing their intellectual property. 

Maybe, ultimately, that would be a good thing.  But that’s by no means clear ... and quite likely not true. Either way, however, this is not the kind of thing you bury in legislation and hope no one notices.

[Full text of the bill is here (PDF).]

[UPDATE May 17, 2013: Apparently, the irony of not being transparent with the contents of your transparency law was just too delicious to pass up, as Markey and his co-sponsors reintroduced the bill yesterday. Once again, the updated press release makes no mention of the protocol requirement.]

Why Study Anything When You Already Know Everything?

If you’re a human being, in possession of one working, standard-issue human brain (and, for the remainder of this post, I’m going to assume you are), it is inevitable that you will fall victim to a wide variety of cognitive biases and mistakes.  Many of these biases result in our feeling much more certain about our knowledge of the world than we have any rational grounds for: from the Availability Heuristic, to the Dunning-Kruger Effect, to Confirmation Bias, there is an increasingly-well-documented system of ways in which we (and yes, that even includes you) become overconfident in our own judgment.

Over the years, scientists have developed a number of tools to help us overcome these biases in order to better understand the world.  In the biological sciences, one of our best tools is the randomized controlled trial (RCT).  In fact, randomization helps minimize biases so well that randomized trials have been suggested as a means of developing better governmental policy.

However, RCTs in general require an investment of time and money, and they need to be somewhat narrowly tailored.  As a result, they frequently become the target of people impatient with the process – especially those who perhaps feel themselves exempt from some of the above biases.

A shining example of this impatience-fortified-by-hubris can be

4 out of 5 Hammer Doctors agree:
the world is 98% nail.

found in a recent “Speaking of Medicine” blog post by Dr Trish Greenhalgh, with the mildly chilling title Less Research is Needed.  In it, the author finds a long list of things she feels to be so obvious that additional studies into them would be frivolous.  Among the things the author knows, beyond a doubt, is that patient education does not work, and electronic medical records are inefficient and unhelpful. 

I admit to being slightly in awe of Dr Greenhalgh’s omniscience in these matters. 

In addition to her “we already know the answer to this” argument, she also mixes in a completely different argument, which is more along the lines of “we’ll never know the answer to this”.  Of course, the upshot of that is identical: why bother conducting studies?  For this argument, she cites the example of coronary artery disease: since a large genomic study found only a small association with CAD heritability, Dr Greenhalgh tells us that any studies of different predictive methods is bound to fail and thus not worth the effort (she specifically mentions “genetic, epigenetic, transcriptomic, proteomic, metabolic and intermediate outcome variables” as things she apparently already knows will not add anything to our understanding of CAD). 

As studies grow more global, and as we adapt to massive increases in computer storage and processing ability, I believe we will see an increase in this type of backlash.  And while physicians can generally be relied on to be at the forefront of the demand for more, not less, evidence, it is quite possible that a vocal minority of physicians will adopt this kind of strongly anti-research stance.  Dr Greenhalgh suggests that she is on the side of “thinking” when she opposes studies, but it is difficult to see this as anything more than an attempt to shut down critical inquiry in favor of deference to experts who are presumed to be fully-informed and bias-free. 

It is worthwhile for those of us engaged in trying to understand the world to be aware of these kinds of threats, and to take them seriously.  Dr Greenhalgh writes glowingly of a 10-year moratorium on research – presumably, we will all simply rely on her expertise to answer our important clinical questions.

A placebo control is not a placebo effect

Following up on yesterday's post regarding a study of placebo-related information, it seems worthwhile to pause and expand on the difference between placebo controls and placebo effects.

The very first sentence of the study paper reflects a common, and rather muddled, belief about placebo-controlled trials:

Placebo groups are used in trials to control for placebo effects, i.e. those changes in a person's health status that result from the meaning and hope the person attributes to a procedure or event in a health care setting.

The best I can say about the above sentence is that in some (not all) trials, this accounts for some (not all) of the rationale for including a placebo group in the study design. 

There is no evidence that “meaning and hope” have any impact on HbA1C levels in patients with diabetes. The placebo effect only goes so far, and certainly doesn’t have much sway over most lab tests.  And yet we still conduct placebo-controlled trials in diabetes, and rightly so. 

To clarify, it may be helpful to break this into two parts:

1. Most trials need a “No Treatment” arm. 
2. Most “No Treatment” arms should be double-blind, which requires use of a placebo.

Let’s take these in order.

We need a “No Treatment” arm:

• Where the natural progression of the disease is variable (e.g., many psychological disorders, such as depression, have ups and downs that are unrelated to treatment).  This is important if we want to measure the proportion of responders – for example, what percentage of diabetes patients got their HbA1C levels below 6.5% on a particular regimen.  We know that some patients will hit that target even without additional intervention, but we won’t know how many unless we include a control group.
• Where the disease is self-limiting.  Given time, many conditions – the flu, allergies, etc. – tend to go away on their own.  Therefore, even an ineffective medication will look like it’s doing something if we simply test it on its own.  We need a control group to measure whether the investigational medication is actually speeding up the time to cure.
• When we are testing the combination of an investigational medication with one or more existing therapies. We have a general sense of how well metformin will work in T2D patients, but the effect will vary from trial to trial.  So if I want to see how well my experimental therapy works when added to metformin, I’ll need a metformin-plus-placebo control arm to be able to measure the additional benefit, if any.

All of the above are especially important when the trial is selecting a group of patients with greater disease severity than average.  The process of “enriching” a trial by excluding patients with mild disease has the benefit of requiring many fewer enrolled patients to demonstrate a clinical effect.  However, it also will have a stronger tendency to exhibit “regression to the mean” for a number of patients, who will exhibit a greater than average improvement during the course of the trial.  A control group accurately measures this regression and helps us measure the true effect size.

So, why include a placebo?  Why not just have a control group of patients receiving no additional treatment?  There are compelling reasons:

• To minimize bias in investigator assessments.  We most often think about placebo arms in relation to patient expectations, but often they are even more valuable in improving the accuracy of physician assessments.  Like all humans, physician investigators interpret evidence in light of their beliefs, and there is substantial evidence that unblinded assessments exaggerate treatment effects – we need the placebo to help maintain investigator blinding.
• To improve patient compliance in the control arm.  If a patient is clearly not receiving an active treatment, it is often very difficult to keep him or her interested and engaged with the trial, especially if the trial requires frequent clinic visits and non-standard procedures (such as blood draws).  Retention in no-treatment trials can be much lower than in placebo-controlled trials, and if it drops low enough, the validity of any results can be thrown into question.
• To accurately gauge adverse events.  Any problem(s) encountered are much more likely to be taken seriously – by both the patient and the investigator – if there is genuine uncertainty about whether the patient is on active treatment.  This leads to much more accurate and reliable reporting of adverse events.

In other words, even if the placebo effect didn’t exist, it would still be necessary and proper to conduct placebo-controlled trials.  The failure to separate “placebo control” from “placebo effect” yields some very muddled thinking (which was the ultimate point of my post yesterday).

Changing the Rules, Ever So Slightly, For Rare Diseases

At the end of last year, US Reps Cliff Stearns (R-FL) and Ed Towns (D-NY) introduced the Unlocking Lifesaving Treatments for Rare-Diseases Act (ULTRA for short). Despite what its bold name might imply (and unlike many recent congressional healthcare bills), ULTRA is actually a modest and carefully-though-out piece of legislation.

The main thrust of ULTRA is to enable developers of drugs for rare diseases to take advantage of the FDA’s existing Accelerated Approval pathway. Accelerated Approval reduces the initial burden of proof for manufacturers to bring a drug to market by conducting smaller clinical trials that measure a drug’s efficacy against “surrogate” endpoints – that is, endpoints that do not directly measure the disease, but rather other factors that are associated with the disease. This can greatly reduce the time and cost of clinical trials.

To qualify for Accelerated Approval, however, trials for a new drug needs to meet two conditions:

• The drug must be studied for treatment of a serious disease, with unmet medical need


• There must be clinical evidence that improving the surrogate endpoint is reasonably likely to predict real benefit for those with the disease

ULTRA does not change the first criterion, only the second. For rare diseases, there is often not robust clinical evidence to support surrogate endpoints, so the bill alters the language slightly to permit the FDA to accept “reasonable scientific data that support and qualify the relevance of the surrogate endpoint”. In essence, the burden to prove the validity of the surrogate has been relaxed, permitting their use in pivotal trials, and using a surrogate may reduce the number of patients needed for a trial by as much as 50-75%.

Accelerated Approval still requires the drug manufacturer to complete full trials to more firmly establish the drug’s efficacy – it just allows the drug to be available on the market while those full trials are being conducted. ULTRA does not change this requirement for drugs of rare diseases, so in the end it is not lowering the standard for these drugs at all.

Obviously, anything can happen to a bill as it wends its way through congress. But as it is currently written, ULTRA is a highly rational, well-targeted adjustment to current law that should quickly show benefits for patients with rare diseases, and deserves quick action and passage.

(Further reading: the FDA Law Blog has an excellent review of the proposed act.)

DDMAC to weigh in on trial design?

The FDA Law Blog has an incredibly interesting entry regarding last week's Untitled Letter from the FDA's Division of Drug Marketing, Advertising, and Communications (DDMAC) to Novartis.

The letter, regarding a detail aid for Novartis's Focalin XR, accuses Novartis of making "unsubstantiated superiority claims" for Focalin XR in comparison to Concerta. What is interesting -- and completely new as far as I can tell -- is that the claims DDMAC are taking exception to are, in fact, primary endpoints of two controlled clinical trials:

Treatment for ADHD consists of symptom relief over an extended time period; thus, ADHD medications must control disease symptoms over the entire treatment course. However, the referenced clinical studies only focused on one specific time point (2 hours post-dose) as the primary efficacy measure in the treatment course of Focalin XR and Concerta. By focusing on the 2 hour post-dose time point, the studies did not account for the different pharmacokinetic profiles and subsequent efficacy profiles associated with Focalin XR and Concerta over the entire treatment course.

So, in essence, DDMAC appears to be taking exception to the trial design, not to Novartis's interpretation of the trial results. This would seem to be a dramatic change in scope.

I am not familiar with the trials in question -- I will post an update with more information shortly. Of special interest to me would be to understand: Were these pivotal trials that played a role in Focalin XR's approval? If so, did the FDA review them in a Special Protocol Assessment (and therefore are two distinct branches of FDA providing divergent opinions on these endpoints)?

Social Networking for Clinical Research

No matter what, negative clinical trial results are sad. We can appreciate, intellectually, that clinical equipoise is important and that negative results are a natural consequence of conducting ethical trials, but it is impossible not to feel disappointed when yet another promising therapy fails to hold up.

However, the negative results published today in Nature Biotechnology on a groundbreaking trial in ALS deserve to be celebrated. The trial was conducted exclusively through PatientsLikeMe, the online medical social network that serves as a forum for patients in all disease areas to “share real-world health experiences.”

According to a very nice write-up in the Wall Street Journal, the trial was conceived and initiated by ALS patients who were part of the PatientsLikeMe ALS site:

Jamie Heywood, chairman and co-founder of PatientsLikeMe, said the idea for the new study came from patients. After the 2008 paper reporting lithium slowed down the disease in 16 ALS patients, some members of the site suggested posting their experiences with the drug in an online spreadsheet to figure out if it was working. PatientsLikeMe offered instead to run a more rigorous observational study with members of the network to increase chances of getting a valid result.

The study included standardized symptom reporting from 596 patients (149 taking lithium and 447 matched controls). After 9 months, the patients taking lithium showed almost no difference in ALS symptoms compared to their controls, and preliminary (negative) results were released in late 2008. Although the trial was not randomized and not blinded – significant methodological issues, to be sure – it is still exciting for a number of reasons.

First, the study was conducted at an incredible rate of speed. Only 9 months elapsed between PatientsLikeMe deploying its tool to users and the release of topline results. In contrast, 2 more traditional, controlled clinical trials that were initiated to verify the first study’s results had not even managed to enroll their first patient during that time. In many cases like this – especially looking at new uses of established, generic drugs – private industry has little incentive to conduct an expensive trial. And academic researchers tend to move a pace that, while not quite glacial, is not as rapid as acutely-suffering patients would like.

(The only concern I have about speed is the time it took to get this paper published. Why was there a 2+ year gap between results and publication?)

Second, this trial represents one of the best uses of “off-label” patient experience that I know of. Many of the physicians I talk to struggle with off-label, patient-initiated treatment: they cannot support it, but it is difficult to argue with a patient when there is so little hard evidence. This trial represents an intelligent path towards tapping into and systematically organizing some of the thousands of individual off-label experiences and producing something clinically useful. As the authors state in the Nature paper:

Positive results from phase 1 and phase 2 trials can lead to changes in patient behavior, particularly when a drug is readily available. [...] The ongoing availability of a surveillance mechanism such as ours might help provide evidence to support or refute self-experimentation.

Ironically, the fact that the trial found no benefit for lithium may have the most far-reaching benefit. A positive trial would have been open to criticism for its inability to compensate for placebo effect. These results run counter to expected placebo effect, lending strong support to the conclusion that it was thoughtfully designed and conducted. I hope this will be immense encouragement to others looking to take this method forward.

A lot has been written over the past 3-4 years about the enormous power of social media to change healthcare as we know it. In general, I have been skeptical of most of these claims, as most of them fail to plausibly explain the connection between "Lots of people on Facebook" and "Improved clinical outcomes". I applaud the patients and staff at PatientsLikeMe for finding a way to work together to break new ground in this area.

People Who Disagree with Me Tend to End Up Being Investigated by the Federal Government

I don’t think this qualifies yet as a trend, but two disturbing announcements came right back to back last week:

First: As you’ve probably heard, KV Pharmaceutical caused quite a stir when they announced the pricing for their old-yet-new drug Makena. In response, Senators Sherrod Brown (D-OH) and Amy Klobuchar (D-MN) sent a letter to the FTC demanding they “initiate a formal investigation into any potential anticompetitive conduct” by KV. In explaining his call for the investigation, Brown notes:

Since KV Pharmaceuticals announced the intended price hike, I called on KV Pharmaceuticals to immediately reconsider their decision, but to this date the company continues to defend this astronomical price increase.

Second: One week after an FDA Advisory Committee voted 13 to 4 to recommend approving Novartis’s COPD drug indacaterol, Public Citizen wrote a letter to the US Office of Human Research Protections requesting the Novartis be investigated for conducting the very trials that supplied the evidence for that vote. The reason? Despite the fact that the FDA requested the trials be placebo controlled, Public Citizen feels that Novartis should not have allowed patients to be on placebo. The letter shows no apparent consideration for the idea that a large number of thoughtful, well-informed people considered the design of these trials and came to the conclusion that they were ethical (not only the FDA, but the independent Institutional Review Boards and Ethics Committees that oversaw each trial). Instead, Public Citizen blithely “look[s] forward to OHRP’s thorough and careful investigation of our allegations.”

The upshot of these two announcements seems to be: “we don’t like what you’re doing, and since we can’t get you to stop, we’ll try to initiate a federal investigation.” Even if neither of these efforts succeed they will still cause the companies involved to spend a significant amount of time and money defending themselves. In fact, maybe that’s the point: neither effort seems like a serious claim that actual laws were broken, but rather just an attempt at intimidation.

Go Green, Recycle your Patients

Euthymics, a small Massachusetts-based biotech, recently announced the start of the TRIADE trial, which they describe as “Phase 2b/3a”. I am guessing that that somewhat-rare designation means they’re hoping that this will count as a pivotal trial, but have not yet had formal agreement from FDA on that topic. Part of this may be due to the trial’s design – per the press release, they’re using a Sequential Parallel Comparison Design (SPCD).

This is an intriguing trial design because it takes one of the benefits of traditional crossover designs – increasing statistical power by “reusing” patients in multiple treatments – while avoiding many of the problems, most notably any concerns about the persistence of treatment effect. This is because only a select but key subset of patients – those who were in the control arm but showed no response – are re-randomized to both arms. This group clearly has no treatment effect to persist, so they make an excellent population to further test with. (It’s important to note that all patients are continued on treatment in order to preserve blinding.)

In essence, we have a placebo run-in phase embedded within a traditional trial. It seems worth asking how this trial design compares against a simpler trial that includes such a run-in – I do not see any information on the website to help answer that.

And that points to the major drawback of the SPCD: it’s patented, and therefore not freely available to study and use. As far as I can tell, the design has not been through an FDA Special Protocol Assessment yet, which would certainly be a critical rite of passage towards greater acceptance. While I can appreciate the inventors’ desire to be rewarded for their creative breakthrough in devising the SPCD (and wish them nothing but good fortune for it), it appears that keeping the design proprietary may slow down efforts to validate and promote its use.