Part XVII · Research methods, evidence, and emerging therapy · Chapter 94

Clinical trials and evidence interpretation

How to read the trials the rest of this book cites, with the non-inferiority margin problem worked out.

1 · Trial phases and development pathways

The phase labels describe a historical development sequence, not what modern trials actually do. Phase I was defined to find a maximum tolerated dose in a small dose-escalating cohort. Phase II was defined to estimate activity. Phase III was defined to compare against standard of care with a definitive endpoint.

That sequence has broken down in three ways, and each has consequences for how you read a paper. First, phase I trials now routinely contain large expansion cohorts that generate the efficacy signal on which approval rests. A trial labelled phase I may have enrolled several hundred patients in disease-specific cohorts. Second, the dose-finding logic of phase I was built for cytotoxics and does not transfer to targeted agents or conjugates, which is the subject of Dose optimization and the move away from maximum tolerated dose. Third, randomisation has moved earlier, so a randomised phase II is now common and the distinction from phase III is one of size and endpoint rather than design.

What to extract from a phase label is therefore limited. Ask instead: was there a control arm, was assignment randomised, was the endpoint assessed blind, and was the analysis pre-specified. Those four questions separate reliable from unreliable evidence more sharply than the phase does. A randomised phase II with blinded central review carries more weight than a single-arm phase III, which is a design that should not exist and occasionally does.

2 · Neoadjuvant, adjuvant, and metastatic design compared

The three settings answer different questions and fail in different ways.

The neoadjuvant setting is fast. The tumour is in place, so response is measurable, and pathological complete response is available within months rather than years. That speed is why the setting carries most early-phase biological work. Its weakness is that the endpoint is a short-term measurement of a long-term question. Endpoints, surrogates, and the overall survival question takes that up.

The adjuvant setting is slow and expensive. Most patients are cured by surgery and the treatment under test, so the events that define the endpoint are rare. A trial needs thousands of patients and years of follow-up to accumulate them. Effect sizes are small in relative terms and can still be large in absolute terms in a high-risk population, which is the distinction drawn in Communication and shared decision-making. The setting is also where overtreatment is generated, because a benefit demonstrated in an enriched population gets applied to an unenriched one.

The metastatic setting has frequent events, so trials read out quickly on progression-free survival. Its characteristic failure is crossover and subsequent therapy, which dilute any overall survival signal. An overall survival difference in a disease with eight available subsequent lines is hard to generate and hard to interpret. That is a real methodological constraint, and it is also the argument most often used to excuse a trial that failed on overall survival. Both things are true.

3 · Biomarker-selected, basket, umbrella, and platform trials

These four designs are frequently conflated and they differ in what they hold constant.

A biomarker-selected trial restricts entry to patients with a marker and tests one intervention. It answers whether the drug works in that population. It cannot answer whether the marker predicts benefit, because there is no marker-negative arm. INAVO120 required a PIK3CA alteration for entry¹. OlympiAD required a germline BRCA mutation². Neither enrolled a marker-negative patient, so neither can distinguish a marker that selects for benefit from a marker that selects for a population which does better anyway.

SOLAR-1 is the design that can make the distinction, and it is worth setting beside them. It randomised 572 patients into two cohorts by tumour PIK3CA mutation status. In the mutated cohort, progression-free survival with alpelisib and fulvestrant against placebo and fulvestrant was 11.0 against 5.7 months, with a hazard ratio of 0.65. In the non-mutated cohort the same comparison gave a hazard ratio of 0.85 with an interval from 0.58 to 1.25³. The marker-negative cohort is what licensed the predictive claim. The approved indication then followed that result rather than any entry criterion, which is a distinction worth keeping when reading how a drug came to be restricted.

A basket trial holds the alteration constant and varies the tumour type. It asks whether the alteration predicts response across histologies. SUMMIT is the breast-relevant example. Basket results are informative when positive across baskets and genuinely ambiguous when positive in one histology, because the alternative explanation is that the histology, not the alteration, carries the response.

An umbrella trial holds the tumour type constant and varies the intervention by alteration. Patients are screened once and allocated to a sub-study. This is an efficiency device, not an inferential one. Each sub-study still needs its own control for a causal claim.

A platform trial is an umbrella with a shared control arm and a rule for adding and dropping arms while the trial runs. I-SPY 2 is the breast archetype, and plasmaMATCH applied the logic to ctDNA-directed allocation. The gain is a shared control and a standing infrastructure, so a new agent enters an existing machine rather than building one⁴.

4 · Adaptive designs and interim decision rules

An adaptive design changes something about itself according to accumulating data, under rules fixed before the first patient enrols. The distinction that matters is between pre-specified adaptation and post-hoc rescue. The first preserves the error rate. The second does not, whatever the paper calls it.

Response-adaptive randomisation shifts allocation toward arms that are performing well. In a platform running many arms this gets more patients onto promising agents and graduates or drops arms faster. I-SPY 2 uses this to estimate the probability that an agent would succeed in a subsequent phase III within a biomarker signature.

Sample size re-estimation adjusts enrolment when the observed control event rate differs from the assumed one. This is the most benign adaptation and also the most often needed, because event rates in adjuvant breast cancer trials have fallen steadily as background therapy improved.

Group sequential designs allow stopping early for efficacy or futility at pre-planned interim analyses, with alpha spent at each look. Two consequences follow and both are routinely ignored. A trial stopped early for efficacy overestimates the effect size, because stopping requires crossing a boundary and random high estimates cross boundaries more readily than random low ones. A trial stopped early also has less safety follow-up and fewer long-term events, so its overall survival estimate is immature by construction, not by accident.

5 · Endpoints, surrogates, and the overall survival question

A surrogate endpoint is intended to substitute for a clinical outcome and predict it⁵. The validation required is not correlation at the patient level. It is that a treatment effect on the surrogate predicts a treatment effect on the outcome, which is a trial-level property and a much higher bar.

Pathological complete response is the clean illustration, and this is where the thread raised in The neoadjuvant setting as a scientific platform resolves. The pooled analysis covered 12 trials and 11,955 patients. Patients achieving pCR defined as ypT0/is ypN0 had better event-free survival, with a hazard ratio of 0.48. Overall survival was also better, with a hazard ratio of 0.36. The association was strongest in triple-negative disease and in HER2-positive hormone-receptor-negative disease treated with trastuzumab. At the trial level, the association between an increase in pCR frequency and event-free survival was essentially absent, with an R-squared of 0.03, and weak for overall survival at 0.24⁶. The authors were explicit that they could not validate pCR as a surrogate.

Both halves of that result are true and they are not in tension. pCR is strongly prognostic for the individual patient. It is not validated as a trial-level surrogate for the treatment effect. A drug that raises pCR is not thereby shown to extend survival. The subsequent I-SPY2 analysis supports the individual-level prognostic claim within signatures⁷. The ctDNA surrogacy question raised in Liquid biopsy and longitudinal monitoring sits at exactly the same point on this scale, and has less trial-level evidence than pCR.

6 · Designing de-escalation trials and the non-inferiority margin problem

This section is the methodological home of every de-escalation claim in this book. The reader error it exists to correct is the conflation of "no statistically significant difference" with "proven equivalent." Those are different claims and only one of them can be established by a superiority trial that failed.

A non-inferiority trial asks whether the smaller treatment is worse by less than a pre-specified margin. The margin is a clinical judgement expressed as a number, and it is chosen before the trial runs. The conclusion is drawn from the confidence interval, not from a P value. Non-inferiority is claimed when the entire confidence interval for the difference lies on the acceptable side of the margin⁸.

Work through IMPORT LOW, and read the margin rather than the result. Partial breast irradiation was compared with whole breast irradiation. The trial was powered to exclude a 2.5% absolute increase in five-year local relapse, with non-inferiority declared if the upper limit of the two-sided 95% confidence interval for the local relapse hazard ratio fell below 2.03. Five-year local relapse was 1.1% with whole breast and 0.5% with partial breast, and non-inferiority was declared⁹.

Now put the margin against the control event rate. A 2.5 percentage point allowance at a control rate of 1.1% permits relapse to more than triple, and the critical hazard ratio of 2.03 says the same thing in ratio form. The trial would have declared non-inferiority had partial breast irradiation doubled the relapse rate. It did not, and the observed absolute difference was minus 0.38 percentage points, so the conclusion is sound. The point is that the conclusion is sound because of what was observed, not because the margin was demanding.

FAST-Forward set its margin more tightly. Assuming a 2% five-year incidence of ipsilateral breast tumour relapse in the control arm, non-inferiority required an excess no greater than 1.6 percentage points, a critical hazard ratio of 1.81. Twenty-six gray in five fractions gave a hazard ratio of 0.67 with an interval from 0.38 to 1.16 against 40 Gy in fifteen¹⁰.

SENOMAC took the structure to axillary surgery and required the upper bound of the confidence interval for recurrence or death to lie below 1.44. Five-year recurrence-free survival was 89.7% against 88.7%, with a country-adjusted hazard ratio of 0.89 and an interval from 0.66 to 1.19¹¹. It also reported per-protocol alongside modified intention-to-treat, which is the analysis discipline the practice block below asks for and which many non-inferiority reports omit.

Now the failure mode. NSABP B-51 reported an invasive recurrence-free interval hazard ratio of 0.88 for regional nodal irradiation against no irradiation, with a confidence interval from 0.60 to 1.28¹². That is a superiority trial that did not demonstrate benefit from irradiation in that population. It is not a demonstration that omitting irradiation is equivalent, and the bound that defeats the equivalence reading is the lower one.

Work out which direction each bound points. Values below 1 favour irradiation, so the interval running down to 0.60 leaves a 40% relative reduction in events from irradiation entirely compatible with these data. That is the size of harm that omission might be causing. The upper bound of 1.28 lies in the direction where irradiation is the worse option, so citing it argues for omission rather than against it. No non-inferiority margin was set in advance and the trial was not powered against one. Reading this result as proof of equivalence is the error this section exists to prevent.

7 · Dose optimization and the move away from maximum tolerated dose

The maximum tolerated dose paradigm assumes that efficacy rises monotonically with exposure and that toxicity is the only constraint. That holds approximately for cytotoxics. It does not hold for targeted agents, where target engagement saturates, nor for antibody-drug conjugates, where the exposure-response relationship for efficacy and for toxicity differ.

The consequence has been visible for a decade. Agents reached approval at doses higher than needed, and the dose was then reduced after marketing. An analysis of novel oncology approvals from 2012 to 2022 found that 78 of 132 drugs, or 59.1%, carried a dosing postmarketing requirement. Requirements asking specifically whether a lower dose would be better have risen recently¹³.

The regulatory response has been to push dose characterisation earlier, with randomised dose comparison before registration rather than after. The practical effect on how you read early-phase data is that a recommended phase II dose derived from three patients per level and a dose-limiting toxicity window of one cycle should be treated as provisional. Chronic toxicity that appears in cycle four does not constrain a decision made on cycle one. For conjugates, where interstitial lung disease and ocular toxicity are cumulative, this gap is not theoretical. The conjugate toxicity data are in Antibody-drug conjugates and targeted delivery.

8 · Statistical and clinical significance are different claims

A P value is a statement about the compatibility of data with a null hypothesis. It is not a measure of effect size, importance, or probability that the hypothesis is true. In a large trial a trivial difference reaches significance. In a small trial an important difference does not.

Three habits follow. Read the confidence interval rather than the P value, because the interval carries the effect size and the precision together. Convert relative effects into absolute ones using the control arm event rate in that trial, since the same hazard ratio means different things at different baseline risks. Ask what the smallest difference worth having would be before looking at what was found.

SONIA is the instructive case. Progression-free survival from randomisation to progression on second-line therapy was 31.0 against 26.8 months and not statistically significant¹⁴, and overall survival was 47.9 against 48.1 months¹⁵. The trial was designed to ask whether first-line CDK4/6 inhibition is necessary rather than whether it works. A result that is not significant on its primary endpoint answers a question about strategy that no significant result would have answered better.

The mirror image is a trial with a significant P value on a difference of two weeks in progression-free survival. Significance there establishes that the difference is unlikely to be chance. It establishes nothing about whether the difference is worth the toxicity.

9 · Representation, generalizability, and equity by design

A trial result generalises to the population that was enrolled. Enrolment in oncology trials is not representative, and the gap is structural rather than attitudinal. A systematic review found that the dominant barriers to participation are structural and clinical rather than refusal. Either no trial was available at the site, or the patient did not meet eligibility criteria¹⁶. Among patients who were offered a trial, participation rates were high and similar across groups.

Reporting is the second failure. In trials supporting cancer drug approvals, race was reported for a minority of trials, and Black and Hispanic patients were substantially underrepresented relative to disease incidence¹⁷.

Both findings point at the same lever. If the constraint is availability and eligibility rather than willingness, the interventions that work are site selection, eligibility criteria that are justified rather than inherited, and removal of the financial and logistical costs of participation. Community outreach aimed at changing minds addresses a barrier that the data do not identify as dominant.

This matters biologically and not only ethically. Differences in tumour biology between populations have been reported, and in nearly all of that work the variable measured was self-reported race rather than genetic ancestry. Ancestry-associated tumor biology, what replicates and what is confounded sets out which of those differences replicate, which attenuate within a subtype, and why calling them ancestry-associated is a substitution the data do not support. Either way the trial consequence is the same. A trial population that excludes the groups in which a subtype is overrepresented produces an effect estimate that may not transfer.

10 · Decentralized and pragmatic conduct

Pragmatic and explanatory trials answer different questions. An explanatory trial asks whether an intervention can work under favourable conditions, with selected patients, intensive monitoring and protocol-defined assessments. A pragmatic trial asks whether it does work under ordinary conditions, with broad eligibility and routine-care follow-up.

Decentralised conduct is a delivery method rather than a design. Remote consent, local laboratory draws, home infusion, shipped oral drug and telehealth visits reduce the travel burden that Representation, generalizability, and equity by design identifies as a barrier. It shifts trials toward the pragmatic end by making participation compatible with ordinary life.

The cost is assessment consistency. Imaging performed locally on varied scanners at varied intervals is noisier than imaging performed centrally to protocol. For a progression-free survival endpoint that noise is not neutral. Assessment schedule differences between arms produce evaluation-time bias, which is why blinded independent central review exists. A decentralised trial with a progression endpoint needs central review more, not less.

The endpoints best suited to decentralised conduct are those that do not depend on scheduled imaging: overall survival, patient-reported outcomes, treatment discontinuation and toxicity.

11 · Regulatory pathways, accelerated approval, and post-marketing evidence

Accelerated approval permits marketing on a surrogate reasonably likely to predict clinical benefit, with a confirmatory trial required afterwards. The design assumes that the confirmatory step functions.

The evidence that it functions is weak. Of 93 cancer drug indications granted accelerated approval between 1992 and 2017, confirmatory trials demonstrated improved overall survival for 19, or 20%. Another 19 confirmed the same surrogate used in the preapproval trial, and 20 reported improvement in a different surrogate. Several confirmatory trials were delayed, pending or ongoing at the time of analysis¹⁸.

In breast cancer this is the live controversy of the current decade. Several conjugate and pathway-inhibitor approvals rest on progression-free survival. Some have subsequently shown overall survival benefit, as ASCENT did at 12.1 against 6.7 months¹⁹ and TROPiCS-02 at 14.4 against 11.2 months²⁰. Others have not, and in the metastatic setting a null overall survival result is genuinely ambiguous for the reasons in Neoadjuvant, adjuvant, and metastatic design compared.

The position this book takes is narrow. Progression-free survival benefit is a real benefit when progression is symptomatic and the toxicity is tolerable. It is not evidence of longer life, and it should not be described to a patient as though it were. The conversation about how to say that accurately is in Communication and shared decision-making.

References

All 20 references

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