Trial design for targeted therapies and immunotherapies
The classical oncology sequence of trials, phase I for toxicity, phase II for activity and phase III for comparison against standard treatment, was built for cytotoxic chemotherapy on the assumption that toxicity and efficacy both rise with dose. Targeted therapies, immunotherapies among them, break that assumption. So trial design for them changes in every phase, in what the phase asks, how large it is and how its patients are selected, and trials take up flexible designs under rules the protocol sets in advance.
Targeted therapies and the classical sequence of trials
Targeted therapies, unlike cytotoxic chemotherapies, block specific pathways or mechanisms by which tumours grow, or stop tumours inhibiting the immune system. They can act on cancer cells or on immune cells, and those acting on immune cells are the immunotherapies.
The classical sequence of oncology trials identifies the maximum tolerated dose and the recommended dose in phase I, selects the most promising molecules on their activity, the response rate, in phase II, and compares them with standard treatment in phase III. Phase II trials assess drug activity and tolerance in usually a few hundred patients, and if the drug shows sufficient activity and reasonable tolerance, phase III trials compare it with existing treatments or placebo in a larger population.
That sequence was developed for cytotoxic chemotherapies, and it is not optimal for targeted therapies. The arrival of targeted therapies, immunotherapies included, has required a re-evaluation of the classical methods used in oncology over the previous 50 years.
The evaluation of targeted therapies can no longer be based on the parallel between dose-toxicity and dose-efficacy. In cytotoxic chemotherapy trials the two are positively correlated, but in targeted therapy trials high doses can sometimes be well tolerated, and increasing the dose beyond a certain level does not increase tumour response.
The tumour response to an immunotherapy depends on the individual patient's immune function, so it does not follow the pattern seen with cytotoxic chemotherapy, which attacks and kills cancer cells directly, so that an increase in dose usually increases efficacy. Immune-targeting agents instead either stimulate immune cells or prevent cancer cells from deactivating the immune response, and with that mechanism of action dose does not always correlate with efficacy.
Phase I: the biologically active dose
A classical phase I study, for cytotoxic chemotherapy, determines the maximum tolerated dose and a recommended phase II dose and obtains an initial safety profile. It assumes that increasing the dose increases both toxicity and activity, and that assumption lets it identify a "therapeutic area" with acceptable toxicity and probable activity. Methods of finding that area include the "3+3" method, which targets a maximum tolerated dose with a toxicity of 33%, that is, two patients out of six having a treatment-related side-effect, and the more flexible continuous reassessment method, which sets a target toxicity level, usually 25% to 30%, before the study starts. The recommended phase II dose is then established from the maximum tolerated dose, often as the dose level just below it.
This method raises issues for targeted therapies, whose dose does not always correlate with toxicity and activity. Because some targeted therapies have low toxicity, the maximum tolerated dose is never reached in about 25% of phase I targeted-therapy studies despite high dose levels, and the toxicity that does occur can be relatively independent of dose. Once the drug's target is saturated, increasing the dose will not usually increase activity. The objective of a phase I targeted-therapy study is a biologically active dose with minimum toxicity, not the maximum tolerated dose sought in a classical phase I study. For immunotherapies, the maximum tolerated dose was never reached in many phase I studies, so the minimum effective dose, the maximum effective dose and the maximum administered dose are more relevant than the maximum tolerated dose for estimating the recommended phase II dose.
The biologically active dose remains theoretical where activity on the target is difficult to measure, particularly where biomarkers of target saturation are not available. Where biomarkers are available, their levels do not always correlate with clinical benefit, which suggests a more complex mode of action than expected. Using them also often requires repetitive tumour sampling, which may not be acceptable. In 2018 less-invasive or non-invasive methods to monitor tumour evolution were being developed: functional imaging, to assess tumour perfusion, heterogeneity and texture and to quantify angiogenesis, and liquid biopsies such as blood sampling, to assess circulating tumour cells. This research may allow drug activity to be evaluated better, independently of toxicity.
A classical phase I was not designed to assess activity, but a phase I targeted-therapy study evaluates tolerance and activity simultaneously. With fewer dose levels and more patients at each level, first-in-human studies are approaching phase II studies. Early clinical trials of targeted therapies need to assess toxicity and give early signals of efficacy simultaneously, based on biomarkers when they are available. A phase I targeted-therapy study still needs to limit its number of patients to a few tens and to limit the number and size of its expansion cohorts.
Phase I expansion cohorts and seamless development
Expansion cohorts established for the most promising dose levels give an idea of tolerance and efficacy in different cancer localisations. In phase I targeted-therapy studies they can reach hundreds and sometimes more than a thousand patients with no a priori decision rules, and their sample sizes are not always justified. A review of 522 phase I studies performed at the Dana-Farber/Harvard Cancer Center found that 60% of those with three or more expansion cohorts had response or activity as an objective without any justification of the sample size.
These cohorts should be designed with the same statistical rigour as classical phase II studies. In phase I immunotherapy studies, whose expansion cohorts often have unjustified sample sizes despite having efficacy as an exploratory objective, that rigour means allowing for false-positive and false-negative results and setting interim futility stopping rules to prevent unethical treatment of patients. The cohorts should also stay at a reasonable size of 10 to 20 patients, with clear statistical decision rules.
The development of cancer immunotherapies has substantially changed the traditional drug development methodology in oncology. The development and approval of pembrolizumab show how that process has accelerated. Oncology phase I trials enrol patients rather than healthy volunteers, for ethical reasons, so drug activity can be explored at that early stage. The first-in-human phase Ib trial of pembrolizumab began in 2011 to identify the recommended phase II dose in patients with advanced solid tumours, but the drug seemed to have a high level of activity, so additional patients were enrolled into melanoma and non-small cell lung cancer cohorts. As more patients were assessed its superior activity became increasingly evident, and additional patients were included in other tumour cohorts. In all, more than 1,200 patients were recruited into the open-label phase Ib trial. In September 2014 the drug obtained marketing approval for metastatic or inoperable melanoma through an accelerated process based on the phase Ib results, and in October 2015 the approval was extended to non-small cell lung cancer patients expressing PD-L1. This seamless development was substantially quicker than the traditional sequence of trials. Although development time is remarkably shorter, the design of immunotherapy studies is challenging in other respects.
Phase II design
Phase II studies aim to establish whether a drug at the biologically active dose has clinical efficacy with sufficient tolerance to continue to phase III. For cytotoxic chemotherapies they are often single-arm studies that assess response rates over a short period. Most phase II oncology studies assess activity on the response rate, the best response obtained or the response at a given time, and their hypotheses are generated from an already established response rate at a given time. The Simon and Fleming designs define a minimum response rate below which the treatment is considered ineffective, and a targeted response rate that indicates enough activity to progress to phase III. Bryant and Day adapted the Simon method to account for efficacy and toxicity simultaneously, so that a treatment is considered not of interest if the response is inadequate or the toxicity excessive. The Bryant and Day method can be used for certain targeted therapies, such as immunotherapies, for combinations of targeted therapies, and for targeted therapies combined with chemotherapy or radiotherapy.
Phase II studies evaluate targeted therapies in patients who will potentially respond to treatment, selected not only on disease characteristics, such as clinical stage and histological type, but also on the tumour's molecular profile and on biomarkers that are, or are suspected to be, predictive of response. Even on a limited number of patients, phase II may identify biomarkers that could predict response. That work is exploratory at this stage of development, and it facilitates later development by increasing understanding of the underlying biology of targeted therapies.
A single-arm design can be considered where the endpoint, progression-free or overall survival at a given time point, has a reliable historical control. In phase II studies of a highly selected population, though, a precise reference or historical control for response, such as a progression-free survival rate, is very difficult to obtain, so a control group is needed to validate the hypotheses and assess activity. But the control group cannot be compared directly with the experimental group, because the limited number of patients in phase II gives insufficient statistical power.
A comparative randomised phase II built on phase III methodology is sometimes proposed. Such studies accept a high false-positive risk, often around 20% and sometimes as high as 40%, to reduce the number of patients required, and accepting that risk means accepting that two out of five significant differences obtained will be by chance. Where a treatment is extremely active the strategy may prove more efficient. Marketing authorisation can be granted without the long and expensive phase III. But a small sample that lacks statistical power also carries a large risk of non-significant and unconvincing results, which may stop the development of an active treatment.
Phase III design
Phase III studies are essential to compare targeted therapies with standard treatment, and the therapies can be evaluated as monotherapy, in combination with other targeted therapies, or alongside standard treatment. Comparison with standard treatment is recommended. Comparing different targeted therapies, or different dosages of the same one, without a control arm is not. The control arm also allows the biomarkers that may predict activity to be evaluated.
Where a biomarker is known or suspected and its status is available at randomisation, the study should be stratified by it, but this is rarely done. No biomarker analyses of EGFR or KRAS were planned in the studies assessing gefitinib in lung cancer or cetuximab in colorectal cancer. Actions were taken retrospectively, or during the study on a portion of the population that was probably not representative. In those studies the benefits of randomisation were probably lost and the results are difficult to interpret.
A phase III targeted-therapy study needs more patients than a phase II but can be limited to a few hundred. The clinical gain observed with targeted therapies, such as the decrease in the risk of progression or relapse, is far superior to that observed with chemotherapy. A reduction in that risk of 40%, a hazard ratio of 0.6, or even 60%, a hazard ratio of 0.4, could be predicted, and the predicted gain is an important parameter in calculating the number of patients required. The gains can be larger still in a highly selected population, for instance patients with a specific tumour mutation matched to the corresponding therapy. Phase III studies traditionally evaluated treatments in broader populations, but phase III targeted-therapy studies are often performed in a biologically homogeneous subpopulation.
Against placebo, randomisation can be unequal, for example two-thirds of patients to the experimental arm and one-third to placebo, which minimises the number of patients exposed to placebo. At equal power it needs about 10% more patients overall, with about 10% to 20% fewer patients receiving placebo, and it evaluates toxicity and efficacy in the experimental arm more precisely.
Phase III targeted-therapy studies begin in advanced-stage disease, as classical phase III chemotherapy studies do, and the new therapies must prove efficacy at advanced and non-advanced stages before being evaluated in patients with a better prognosis, in the adjuvant or neoadjuvant setting. With targeted therapies it cannot be assumed that results in metastatic disease will extrapolate to a less advanced stage, such as adjuvant treatment after surgery, as the antiangiogenic studies in localised colorectal cancer showed.
Interim analyses of efficacy and futility should be done according to strict rules under the control of independent expert committees, which may allow an early conclusion and publication of the result, positive or negative. Futility analyses allow the early termination of studies that have an extremely small chance of showing treatment efficacy.
Adaptive and flexible designs
Phase III trials with more homogeneous targeted populations use more flexible designs, including interim analyses and adaptive designs, which allow the sample size, and sometimes the trial design, to be modified during the trial. Interim analyses are a first step toward more flexible methods. Adaptive randomisation modifies the treatment allocation ratio on the basis of interim results, so that if the treatment in one arm proves more active at an interim analysis, more patients can be randomised to it. Although this appears promising, it is controversial among statisticians, because the modifications may extend the study duration and introduce biases. If the protocol allows for it at design, sample size can be adjusted from interim results reviewed by an independent expert committee, and using the treatment effect estimated at an interim analysis most frequently increases the number of patients to be included.
Enrichment continually selects a population in which the treatment may be more effective. In a checkpoint inhibitor study, for instance, only patients with strong PD-L1 expression in the stroma can be included, or that subpopulation can be reinforced by calculating a specific power for it. Such a design can use a closed testing procedure, which ranks the tests hierarchically, for example testing the treatment effect in the enriched subpopulation only if the benefit is globally significant. These methods can rest on biomarkers strongly suspected to be related to efficacy, but in a number of cases no such biomarker is available. A "therapeutic test" is another option: all patients are treated with the targeted therapy, and only those who respond or remain stable are randomised in a second phase. Comparing responders and non-responders in the initial phase may identify new biomarkers.
A combined phase II–III design starts as a randomised phase II that extends into a phase III if the phase II results are positive, and the phase II patients are included in the phase III analysis. Some trials go beyond the classification of cancers by localisation and histological type, using molecular anomalies to classify patients and proposing for each the targeted therapy best adapted to their profile. Pilot studies of this kind, such as SHIVA, raise their own methodological questions: how many targeted treatments, what combination of strategies, what stopping rules, how to introduce new treatment arms, and how the resulting data can be analysed to extract knowledge that can be trusted.
In phases I and II, a joint evaluation of tolerance and efficacy has become necessary as soon as the optimal dose is established. These phases need to establish the therapeutic dose rapidly and provide initial efficacy information. Adaptive designs can also be considered for the early phases. Toxicity is relatively independent of tumour localisation and histological type, but efficacy cannot be dissociated from them, so a sufficient number of patients with the same tumour type has to be treated early. In such a design, patients are randomised across several treatment arms at different dose levels and a control arm, with tumour types equilibrated across arms to give an initial idea of efficacy. Interim analyses select one or more experimental arms on tolerance and biological criteria of efficacy. Inclusions can continue in the two or three most promising arms and in the tumour types that appear most sensitive, and these expansion cohorts, of a reasonable size, support a decision on whether to proceed to a randomised phase II with a more robust criterion such as progression-free survival.
Precision oncology, built on the known molecular anomalies of tumours and the therapies that target them, has substantially modified the methods developed to evaluate cytotoxic chemotherapies. Randomised phase II studies evaluate the degree of treatment activity and allow smaller phase III studies to be designed. The flexible methodology of a randomised phase III allows the initial hypotheses to be re-evaluated during the study, and the sample size and inclusion criteria to be modified to select the patients more likely to benefit. Where these more flexible methods are permitted, the study conception and the rules for applying them must be clearly defined in the protocol at the design stage. Only a strict methodology based on early randomised studies, starting from phase II, can optimise the evaluation of the large number of targeted therapies and their combinations so that each patient can receive the treatment best adapted to their tumour's biological profile.
Immunotherapy trials: patient selection and late toxicity
Patient selection is vital in immunotherapy studies. Despite the high activity of agents such as pembrolizumab and nivolumab in certain cancers, only a minority of patients have long-lasting remissions, and given the toxicity profile, careful identification and selection of the patients expected to benefit has become essential. Patients with a pre-existing immune response and more inflamed tumours tend to respond better.
The onset of immune-related adverse events is often delayed, some beginning as long as a year after treatment. A clinical trial design should allow for the long-term collection of toxicity data and the assessment of possible relatedness to the immunotherapy. This is achievable in most cancer studies because extended patient follow-up is usually incorporated to evaluate the overall survival benefit.