Add-on or step-up trials for new drug development in rheumatoid arthritis: A new standard?
Article first published online: 3 JUN 2003
Copyright © 2003 by the American College of Rheumatology
Arthritis & Rheumatism
Volume 48, Issue 6, pages 1481–1483, June 2003
How to Cite
Boers, M. (2003), Add-on or step-up trials for new drug development in rheumatoid arthritis: A new standard?. Arthritis & Rheumatism, 48: 1481–1483. doi: 10.1002/art.11141
- Issue published online: 3 JUN 2003
- Article first published online: 3 JUN 2003
- Manuscript Accepted: 12 MAR 2003
- Manuscript Received: 29 JAN 2003
The last few years have seen a remarkable increase in the number of trials of therapies for rheumatoid arthritis (RA). In large part this reflects highly successful drug development programs that have brought us leflunomide and cytokine inhibitors such as anti–tumor necrosis factor and interleukin-1 receptor antagonist, with many more products still in the pipeline. Interestingly, one trial design is becoming the standard, especially for new biologic agents: a comparison of new drug or placebo added to ongoing disease-modifying antirheumatic drug (DMARD) treatment—usually methotrexate (MTX)—in a population of so-called “partial responders.” This “add-on” or “step-up” design has obvious appeal, but proponents appear unaware of its disadvantages. Herein I will try to enumerate the pros and cons of the design and to propose (partial) solutions.
In an add-on or step-up combination trial, patients who have active disease despite stable treatment with a DMARD are selected. These patients are then randomized to receive the test drug or placebo. The add-on design differs from the parallel design in which the study drugs are started simultaneously, and from the step-down approach in which the drugs are started in parallel, but drugs included in the combination are discontinued at fixed periods during the trial. The main focus of this article is aimed at trials testing new drugs in MTX partial responders. However, all of the points discussed may apply as well to trials in patients who are partial responders to other concomitant therapies, such as nonsteroidal antiinflammatory drugs (NSAIDs) and glucocorticoids.
Add-on trials have both practical and theoretical advantages. Practical advantages include the absence of flares that may result from stopping other therapies, benefiting the patient and facilitating inclusion; and the correspondence of the add-on to what is often already done in daily practice, although it is unclear whether practice has driven trial design or vice versa. Also, in certain cases the addition or maintenance of concomitant drug may have specific benefits (e.g., MTX may inhibit formation of antibodies directed against infliximab). Further, regulatory agencies routinely require a placebo-controlled trial to prove efficacy of a drug (“proof of concept”). These agencies accept an add-on trial as a means to provide such proof. Theoretically, the add-on strategy can be advantageous in cases in which the single drugs affect different aspects of the disease. For example, in the case of a new drug that slows radiographic progression but does not improve clinical symptoms, the add-on design would be ideally suited to study whether the addition of this drug is useful in patients with early RA who have had progression of radiographic features with standard treatment despite control of disease activity.
One important disadvantage of the add-on design in the proof-of-concept stage is that two concepts are being tested simultaneously: 1) efficacy of the experimental drug; and 2) efficacy of the combination with the background drug. Because the trial patients have already had a suboptimal response (or lack of response) to one agent, only limited information on any potential benefit of the combination will likely be obtained. Therefore, if the group receiving the combination treatment fares better, it is unwise to conclude that the combination is better than the test drug working alone. When this design is extended to phase III trials, newer therapies nevertheless become “wedded” to their comedication, unless new monotherapy trials are subsequently performed. Importantly, unknown drug–drug interactions increase the potential for toxicity in the active treatment arm and at the same time complicate interpretation of any side effects because the experimental drug is not given as monotherapy.
An example from the field of microbiology may help to further clarify these key points. Consider cotrimoxazole, an effective combination of sulfamethoxazole and trimethoprim. In cotrimoxazole, these drugs can work synergistically and bactericidally, whereas each component given singly is only bacteriostatic. Synergism occurs because each component attacks a different part of an important enzyme pathway, blocking “escape” enzyme activity. When an infection is caused by microorganisms that are partially resistant to either or both of the components, starting one agent and adding the second in case of insufficient response may not control the infection, whereas immediately starting with the combination would have a better chance of success. When the add-on does work, we remain unsure whether it was the added drug or the combination to which the success can be attributed.
Another disadvantage is that the concept of “partial response” has not been properly defined. Patients in recent add-on trials have invariably had very active disease at baseline (e.g., erythrocyte sedimentation rates of ≥50 mm/hour, ≥25 painful and swollen joints, etc.). “Therapy failure” or “nonresponse” would be a more appropriate term for their situation, and this begs the question whether such patients are really at risk of a flare. However, selecting patients who are truly “partial responders” would decrease the efficiency of the trial. With only moderate disease activity, the potential to improve is reduced, thus making it more difficult to distinguish between the effects of active and control treatments. A final, more general problem with trials that require “partial response” or “failure” with previous therapy is that this criterion selects for patients who are less likely to respond to any therapy. Unfortunately, in the proof-of-concept stage this problem is hard to avoid, because such studies usually have to be performed in patients who have been treated unsuccessfully with multiple antirheumatic drugs.
Apart from these specific disadvantages of the add-on design, there are further drawbacks. If we admit that addition of placebo to continued suboptimal or ineffective treatment comes close to true placebo treatment, all the disadvantages of placebo apply. First, with so many effective agents available, most rheumatologists now feel uncomfortable with the idea of leaving patients with active RA untreated for long periods of time, although a maximum of 12 weeks may be acceptable. Second, from a methodologic point of view, placebo-controlled trials are suboptimal where effective treatment exists, because a large proportion of patients in the placebo group will drop out early due to inefficacy; this will destroy the balance in prognosis between the trial groups created by randomization. As these dropouts are subsequently started on alternative therapy (or are even offered the experimental drug!), a sound comparison based on intent to treat becomes more and more difficult.
What about other concomitant therapy, specifically NSAIDs and glucocorticoids? Even in monotherapy trials, concomitant NSAID therapy is almost universal. NSAIDs can be seen as drugs with only mild-to-moderate antiinflammatory efficacy, but the problem is greater with glucocorticoids: these are potent antiinflammatory agents with true disease-modifying properties. Both NSAIDs and glucocorticoids have their own spectrum of toxicity. Thus, any trial that allows such “background” therapy with these drugs should be recognized as being de facto an add-on combination trial.
What are the solutions? If in the proof-of-concept stage a comparison with placebo is required, one should be up-front in the design and use a true placebo group, in which prior therapy has been stopped. As stated above, the duration of the placebo period in active RA should probably not extend beyond 12 weeks. To enhance inclusion, patients receiving placebo might be offered the active drug after the 12-week period, creating a before/after design in this group that may add to the proof of concept. Although such a procedure causes irreparable contamination (exposure of one group to the treatment received by the other group), any longer-term comparison with a depleted placebo group (caused by the large dropout rate) is probably of limited use anyway. When concern about flares remains an issue, washout periods could be limited to the time needed to dispose of the previous DMARD, or this drug could even be tapered more slowly during the trial instead of stopped before trial start. In patients who have a flare during the trial period, the treatment should be regarded as a failure.
If true placebo is not possible and an add-on design cannot be avoided, a third trial arm could be designed with the experimental drug as monotherapy. For example, in a trial of new drug “Z,” MTX partial responders would receive 1) true MTX plus placebo Z (“placebo group”); 2) true MTX plus true Z (“add-on” group); 3) placebo MTX plus true Z (“Z monotherapy group”). This at least would enable comparisons with a “pure” treatment group. The scope of the trial could also be broadened to include patients with active RA taking any of the most popular drugs, or even regardless of concomitant therapy, as long as the regimen is maintained during the trial period. Such a design would enhance inclusion and decrease the chance of an unexpected toxic interaction occurring in a large proportion of patients in the experimental group. In other words, as different concurrent drugs are allowed, it is less likely that an unexpected negative interaction (reduced effect or increased toxicity) occurring with one of the concomitant DMARDs will spoil the trial. In this design it becomes crucial to apply stratified randomization so that the interventions (experimental or placebo) are balanced across the different concomitant medications.
When the primary interest is the combination, the ideal trial setup is a parallel-group design with patients who have not taken any of the components, where a group either receives one component singly, or the combination. In such trials, the add-on strategy could also be compared head-to-head with a parallel strategy.
In conclusion, I have tried to review the arguments for and against an add-on design, especially in the proof-of-concept stage of new antirheumatic therapy. Although attractive and popular, this design is in fact inefficient for such proof (of efficacy), and results are difficult to interpret with regard to toxicity. Further, the design is potentially harmful since patients are exposed to a combination with unknown toxicity where proof-of-concept for the single drug has not yet been obtained. Finally, like true placebo-controlled trials, the design is probably unethical and its results hard to interpret if trial duration extends beyond 12 weeks. Alternatives include returning to a short but true placebo phase, adding an arm in which the experimental drug is applied as monotherapy, or broadening inclusion to all patients with active RA regardless of concomitant therapy. The true value of any combination strategy is best studied in head-to-head trials with the components started simultaneously or as single drug.