in ,

“Not-so-random” thoughts on what you need to know about Clinical Trials

Authors: Research Action Group (RAG) AMMA Education Research Foundation

Clinical Trials- Phases

There are several phases a “new” drug goes through prior to becoming recommended practice.

Thus, a new drug does not enter the market straight away and is not prescribed without prior testing.

There are several steps before the drug enters the market and some after the drug enters the market.

The pre-phase I studies

A new compound or a new molecule (or intervention) is not immediately tested on humans.

There are several reasons for this. The new compound or molecule may not, despite the best intentions of the “creators”, behave as expected and may possibly lead to serious adverse events.  Therefore, the process of extensive testing of new drugs or therapeutic interventions starts in animals in a lab setting.

Animal studies look at several things

  1. We quantify or assess the course of the molecule (drug), over time, in various tissues and organs –pharmacokinetics
  2. We determine the effects of the molecule (drug) on the structure and function of cells, tissues, organs, and organ systems – pharmacodynamics
  3. We assess what happens to the molecule- how is it metabolized, what is it converted to, how or how much is retained, how is it excreted, what are the effects of these conversions, are these conversions/storage/excretions toxic or adverse event inducing changes.
  4. We give the molecule in increasing doses till it kills at least 50% of the lab animals to determine the lethal dosage (LD50 ). We examine the X% (usually 50%) that die at once. Survivors are killed at various intervals thereafter and examined.

We will consider the new molecule for further testing if

  • The lethal dose (LD50) of the new molecule is much higher than the dose required for the desired pharmacodynamic effect (in other words, the molecule can do good at much lower doses than when it becomes lethal)
  • if other attributes that are tested are favourable- there are more beneficial changes than toxic effects
  • if the further development and testing of the molecule shows promise to provide an affordable (or more profitable) drug

Further testing is done on humans based on the results of the animal studies that precede it.

Phase I trials

In these trials, tiny or small doses of the compound or molecule is given to a few volunteers (variable number, maybe 10-15) to see how the molecule behaves in healthy humans.  This step focuses on examining if the molecule or compound displays the same pharmacokinetics, the same metabolic conversions and for any potential toxicity.

If the molecule behaves safely, the molecule is then given in increasing amounts (incremental increases) to volunteers or subjects until the results (pharmacodynamic results) found in animals are replicated in humans. This phase of the testing may be done on healthy subjects or on persons with the serious forms of the disease or condition (who are not improving with any of the available current interventions) that the molecule is expected to improve.  These subjects undergo intense monitoring for known and unknown side effects and a whole series of lab tests for a whole range of values.

If the molecule or compound still looks promising, we move onto phase II trials

Phase II trials

In a phase II trial, the molecule or compound is administered to a larger group of participants (maybe between 25-40) with the target condition of interest.

This phase aims

  • To confirm the results of the previous pharmacokinetic and metabolic studies
  • To determine and confirm the dose required to achieve the optimal or desired pharmacodynamic effects
  • To estimate the proportion of persons who respond and achieve the desired effects at the set dose and the proportion of persons who do not respond and do not achieve the desired effects at the set dose
  • To look for known and hitherto unknown effects of the molecule (toxicity) on a larger sample.

Phase III trials

Molecules or compounds that still look promising in phase II trials may be continued to phase III trials.

It is important to consider that not all molecules in a phase II trial may continue to a phase III trial even if they look promising. Issues of cost, development and return on investment play a role in further progress.

Do all phase II “passed” molecules or compounds achieve success in a phase III study? A moot point that may need further study. (Intuitively, it is unlikely a significant proportion will achieve success).

The phase III trial is a full-fledged randomized clinical trial with sufficient sample size and power to either conclusively prove or refute the predicted benefits from the molecule.

Phase IV studies

These are otherwise known as surveillance studies or post marketing studies. Needless to say, they occur after a phase III study has proven benefits and the molecule or compound is now into the realm of prescription and marketing.

Why do we need phase IV studies?

  • We need to continue surveillance to look for rare, serious adverse events that may not have shown up in the subjects studied earlier
  • If we want to be 95% confident or sure of observing one adverse event that occurs once in X subjects, we need to study at least 3X subjects.
  • The sample size estimation for phase III trials are rarely so large and hence we need phase IV studies.
  • We can explore for potential interactions of the molecule with other drugs, diet, behaviors, the distribution or determinants of its use (pharmacoepidemiology) and health economics- measurement of cost effectiveness, cost utility (pharmacoeconomics).
  • We can also explore for the effects of the drug in a wider spectrum of population that may not be sampled as part of a phase III trial (the elderly, the young, vulnerable populations) etc.

Take home messages

  • There is a process of development before a molecule enters the market for prescription towards a disease or condition
  • The initial phase of testing is usually done on animals in captive conditions in a lab. Lives are lost to look for solutions to human problems…so, if you have ever popped a pill, please do attempt to be more humane towards animals.
  • Studies pass through progressively larger numbers and strict protocols before they are finally approved for marketing.
  • Data on post marketing studies have to be considered before the drug/molecule/compound is finally declared relatively safe for use.

Ideal or Pragmatic Clinical Trial?

We have looked at the various phases of trials that are done during the development of a molecule into a drug or medicine.  We have seen how these are tested on a larger population as part of a randomized clinical trial (phase III trials). A randomized clinical trial (RCT) is considered the best design to determine the efficacy or effectiveness of a new intervention.

Clinicians worldwide are aware that the strictly controlled environment of a RCT does not necessarily translate to actual clinical practice. It may not be possible to monitor patients as intensely as done during a trial, patients may or may not take the medicine as prescribed, and they may or may not come for follow up, and may or may not report adverse events.  In other words, the “effectiveness” or “efficacy” of an intervention with evidence from a well-designed RCT may or may not translate to actual benefits in clinical practice.

Why does that happen?

Typically, these trials are designed and carried out adhering to a strict protocol that is designed to tell us if the new intervention (drug) are taken faithfully by subjects (after prescription) will exhibit their full pharmacodynamic properties, have an acceptable low risk of adverse events, and do more good than harm. The RCT is done under a strictly controlled environment that is more ideal than pragmatic. Thus, the RCT is designed to find out if the new drug can provide better than harm under ideal conditions….it may not be able to provide an answer to the benefits accrued under less than ideal conditions.

RCTs usually (an ideal RCT)

  • Have strict exclusion and inclusion criteria. These criteria are usually defined with strict and narrow parameters that limit inclusion to the high or moderate risk subjects. Subjects on the milder spectrum of the condition may be excluded just by the parameters of the inclusion criteria.  A particular subgroup, with a different risk profile, may also be excluded just because it is difficult to make assessments in those groups (example-studies on pregnant women often do not included multiple pregnancy as a subgroup) or because those are relatively rarer.
  • Enrol subjects who are committed to complete the course of medication. This may limit enrolment to within a geographical radius that allows us to follow them up more intensely, where we could possibly chase them down at their residence if they do not turn up.
  • Exclude subjects who are later found not to meet the criteria for inclusion (after enrolment)
  • Include subjects who show they can withstand or are more likely to withstand the new treatment, thus the extremes of ages (elderly and young) and other vulnerable populations (undernourished or the people with more severe forms of the condition for example) may be excluded from the scope of the trial
  • Subjects are assessed by experts and receive care under the supervision of experts
  • They are carefully and intensely monitored by experts for compliance and health status
  • Assessments may include sophisticated technology and techniques that help to identify adverse events early
  • Have monitors who intervene if compliance fails
  • Have monitors who intervene if the treating doctors do not follow the protocol
  • Look for adverse events focused on the research question- other adverse events may not be reported unless serious
  • Exclude subjects who stop complying
  • Exclude subjects who do not follow up
  • Stop follow up after the duration set by the trial.

What happens in a real life clinical practice?

In real life, a controlled environment does not always exist for clinical practice.

The population with the disease may include the elderly, the young, other vulnerable populations, and people with milder forms or very severe forms of the disease. The methods of assessment may differ. Some clinicians may base their diagnosis on a clinical exam with little tech support, some may base their diagnosis after a very detailed (maybe even an overkill) set of tests including sophisticated scans. People may or may not comply with the medications. People may not comply with follow up and may come at different durations than advised. There may be no one to monitor and point out missed parameters to the treating physician or to the patient. The course, duration and outcomes of the disease may not show the same improvement reported in the trial.

Clinicians become disappointed with the effect of the new medication and wonder if they were sold a dud…and wonder about the integrity of the trial.

What do clinicians want?

Clinicians want to know how a drug or medicine will behave, when prescribed in a small practice (not in the biggest of the institutes that have the most sophisticated diagnostic and therapeutic support)  to patients with a wide spectrum of disease that is often skewed towards the milder forms, and who may or may not come for further follow up. Clinicians want to know what may be a safe dose to get enough of the drug into the body to provide a beneficial effect with minimal or no side effects.

An ideal RCT may or may not be able to answer that question.

What is needed to answer that question is a pragmatic trial focused on the real life management of patients.

pragmatic trial can be designed

  • By setting less strict parameters or boundaries for the inclusion or exclusion of subjects
  • Include all eligible subjects regardless of risk, potential compliance, responsiveness, or site of care
  • Retain all admitted or enrolled subject in the analysis
  • Leave the clinician and the patient to get on with the treatment without intense monitoring or forcing the patient or the clinician to a precise regime
  • Look at a broad range of events and include them in the analysis
  • Charge adverse events to the intervention they were randomized to or received.
CharacteristicIdeal RCTPragmatic RCT
Condition of the trialDoes the treatment work under ideal conditions?Does the treatment work under usual conditions?
Who is eligible?Very strict inclusion and exclusion criteriaAll persons with the target disorder who consent to participate
What happens to subjects found ineligible at a later date?Excluded from the analysisIncluded in the analysis
Administration of interventionBy experts under strict supervised conditions and monitoredAs in routine clinical care
Follow upIntense, frequent visitsAs in routine clinical care
ComplianceClosely monitored with strategies to improve or maintain complianceUnobtrusive monitoring, no compliance enhancing strategies
Adherence to study protocolStrict, monitoredLittle or no monitoring
Reporting adverse eventsRestricted to study question (s)All adverse events
Duration of follow upStops when event of interest occursContinues till the end of trial or death, whichever comes first

Do the conclusions differ in an Ideal and a Pragmatic RCT?

We can conclude from a RCT that

  1. Benefits are clearly greater than harm
  2. Benefits are clearly not greater than harm

How does an ideal and pragmatic RCT differ in the ability to interpret these conclusions?

Type of TrialConclusion from the trial
Benefit > HarmBenefit <= Harm
IdealIt works only if patients and clinicians are willing to walk the extra mile to sustain successAbandon the treatment. It does not work as well as hoped for
PragmaticClearly worthwhile to adopt the treatment as it works under almost all conditionsCannot be sure why it failed – Is the treatment really not good or most patients and clinicians did not follow instructions and hence we could not really evaluate the treatment.

Take Home messages

  •  It is possible to do an ideal RCT or a pragmatic RCT. Both have certain advantages and disadvantages.
  • Both are not exactly in isolation from each other, there may be a certain overlap.
  • The choice of the design (ideal or RCT) depends on the research question. Thus, your research question determines the choice of an ideal RCT or a pragmatic RCT.
  • We could choose to initially test the new treatment under strict conditions using an Ideal RCT design and follow that up with a larger, simpler, pragmatic trial (if the strict trial shows benefits). However, most trials stop at the ideal RCT stage….
  • We could also do a simultaneous ideal-pragmatic design. We start with an ideal RCT design that includes eligible subjects who meet a strict inclusion-exclusion criteria. They are randomized to the intervention arms. Simultaneously, those found ineligible (as per the strict inclusion-exclusion criteria) are included as a separate pragmatic arm and randomized to each intervention. The final analysis can include an analysis of the ideal RCT plus an analysis of the larger group (ideal + pragmatic). (Read more on this design at Bannerjee SH, Raskob G, Hull RD. A new design to permit the simultaneous performance of explanatory and management randomized clinical trials. Clin Res 1984; 32: 543 A)


Clinicians like to have the answers to three questions before they use a new treatment for their patients.

  1. Is the new treatment better than existing treatments?
  2. If the new treatment is not better than the existing treatment, is it at least as good as the existing treatment?
  3. Is the new treatment affordable, does it have fewer side effects or less severe side effects, is it easily available?

These questions can be answered by a superiority or non-inferiority trial design.

superiority RCT attempts to answer the question whether intervention X is superior to an established effective therapy or a placebo (we will discuss effective established therapy later). The margin of superiority is predetermined prior to the trial and is considered as the margin of superiority to be considered as clinically significant.

Example– I will consider intervention Y to be superior to the established Intervention X if the results with intervention Y are at least 15% better than intervention X for specified outcomes.

The margin of superiority is a clinical decision based on optimal benefits to the patients. We can consider these as minimally important differences (MID) and have to incorporate these at the design state of the trial. We will discuss about minimally important differences later.

Any intervention compared to a placebo has to pass through a superiority trial.

non inferiority trial, on the other hand, checks to find if the intervention Y is at least as good as intervention X. The margins of “as good as” are predetermined based on what is clinically significant. Intervention X maybe better (based on the predetermined margin) or worse (based on the predetermined margin) that intervention Y. Essentially, we are checking to see if both interventions are nearly similar and if the dissimilarity is clinically acceptable.

Example– Intervention Y is not inferior to intervention X; Intervention Y may give up to 5% different results in either direction (up to 5% better or up to 5% worse) compared to intervention Y.  Specify the margins prior to the trial.

We can use a non-inferiority design to compare a new intervention against an established therapy. This is most often used to compare a new similar class drug against a market competitor (the interest in this instance is not necessarily to show superiority of drug but that the drug is not inferior to the existing drug)

Take home messages

  1. Clinical trials can explore if an intervention is superior to the existing intervention- superiority trials
  2. Clinical trials can explore if an intervention is not inferior to the existing intervention- non inferiority trials
  3. The margins of superiority or non-inferiority have to be set prior to the start of the trial. These margins play a role in sample size determinations
  4. Any placebo trial (placebos are used only in specific circumstances) has to be a superiority trial. We do not want to show that the intervention is not inferior to a placebo.
  5. More of the same, under different guises, need not always be good (though there may be advantages as in generic drugs), so evaluate non inferiority trials carefully.

Allocate Intervention

A clinical trial compares the effects of an intervention to one or more other interventions. The interventions are offered to groups of eligible, enrolled subjects and the effects compared across groups (or individuals, organs).  To minimize noise in the comparison, the experimental therapy is given to everyone in the “experimental” group and to no one in the control group. Both groups are treated similarly except for the intervention (as much as possible). The outcomes including adverse events are measured and assessed similarly for the two groups.

How do we allocate subjects to the intervention arms?

There are several strategies that can be used to allocate individuals to the intervention arms. We can toss a coin, we can use an “alternate approach (odd and even numbers), we can use days of the week, we can use hours of the day…and several such approaches.

There are several concerns we would like to address while we allocate subjects. An important consideration is that every subject in the trial has an equal, unbiased chance of receiving either intervention. Neither the subject nor the investigator determine the intervention they receive.  Once eligibility is confirmed and the subject is enrolled into the trial, they should have an equal unbiased chance of receiving any of the interventions under study.

How is this achieved?

We can provide each enrolled subject with an equal and unbiased chance to receive any of the study interventions through a process of random allocation.  Subjects are randomly allocated to the intervention arms and this process is not investigator dependent.  There are several strategies for randomization including a simple random allocation, using random number sequences etc. Computer software is available to generate randomization sequences based on several conditions.

We can choose to allocate subjects equally between the intervention arms. Thus, the number of subjects in each intervention arm will be equal (a 1:1 ratio). If we are not sure of the benefits of the experimental therapy, we can choose to have more subjects in the experimental intervention arm and opt for a 2:1 or 3: 1 ratio (ratio of experimental therapy to control therapy).  We could choose to use random blocks – the first block of numbers are allocated to one arm, the second block to another arm and so on. We could choose to have blocks of equal length (example, each block if of 10 subjects) or blocks of unequal length. We could choose to randomize within blocks for better effect.

We also need to have a strategy where (optimally)

  • The subject is not aware of the which intervention they receive
  • The investigator is not aware of which intervention the subject receives or cannot decide which intervention the subject should receive

Thus, allocation is concealed from both the investigator and the subject.

How is allocation concealed?

The schedule for each subject is predetermined based on the randomization generated, noted and placed in a sealed opaque envelope that cannot be visualized until it is open. The envelope is opened by an independent (not connected to the study) person just prior to allocation.

We could have a central office that maintains the randomization schedule. Once eligibility is confirmed and the subject is enrolled, the central office is contacted at the time of allocation and information on the allocation arm is obtained.  We could have differing variations of the central office theme.

We could have the “treatment boxes” arranged in a predetermined random order and just administer the next “treatment box” in sequential order as subjects enter the study.

Why is allocation concealment important?

  • When either the subject or the investigator is “certain” that one of the interventions is better than the other, they may consciously or unconsciously take steps to see that they get allocated to the intervention of choice. The investigator may consciously or unconsciously allocate persons with a lower risk to the preferred intervention. This can bias the results of the trial.
  • The other intervention is the study may be unequally applied once the allocation is known. Subjects in the experimental arm may receive more stringent “co-interventions” while those in the control arms may not receive interventions in the same manner. This may bias outcomes of the trial
  • The “softer” or “milder” outcomes may be reported differently (or assessed differently) based on the investigator or subject preferences about the study intervention and may bias outcomes of the trial

Cluster randomization: In this design, a cluster or group of persons is randomized to a particular intervention (as opposed to individuals randomized).  For example, we can randomize a particular hospital, or a village, or a community, to a particular intervention. Every eligible enrolled person in that cluster receives one intervention.

Allocation between organs: We can choose to allocate between organs since there are certain pairs of organs in humans (Example, eyes, ears, hands, limbs). If we are convinced that the effects of the intervention are locally specific to the organ, we can choose to study both pairs of organs in the same person. This will reduce inter-person noise in the analysis. Example, we could choose to study the effects of laser therapy for retinopathy of prematurity between eyes of the same baby (randomly allocating one eye to receive laser and the other eye to be the control).

Allocation in paired sequential trials: We could randomize between pairs of persons, thus the first person in a pair is randomly allocated to one arm and the other person in the pair receives the other treatment. The results are initially compared between the pairs and then across the entire group of pairs.

Allocation by randomized consent: Subjects are allocated to the different intervention arms prior to informed consent. These are otherwise called as “Zelen” trials and developed as a strategy as some clinicians were worried that the informed consent process impeded the patient-physician relationship and patient recruitment.

Allocation adapted to outcomes: In these trials, the allocation ratio is adapted based on the outcomes of the previously enrolled subject. Thus, if the previously enrolled subject has a good outcome with the experimental therapy, the next subject may receive the experimental therapy. A risky approach that can potentially affect trial integrity and not useful for trials with a “long” interval between intervention and outcome.

Stratification for prognostic factors before randomization: The balance of prognostic factors in the intervention arms can differ, sometimes minimally, sometimes greatly, if randomization is truly random. Although the random process attempts to minimize such differences, it is possible just by chance that there are large differences between the randomly allocated groups. We could stratify important prognostic factors and randomize allocation within each such stratum to achieve better balance of prognostic factors between groups. We can also use a strategy of minimization to achieve balance of prognostic factors between groups.

Allocation to multiple treatments: We can use a factorial design to allocate subjects in a trial with multiple intervention arms. Outcomes can be made dichotomous and compared between multiple intervention arms in the same design.


We have looked at the allocation of subjects in a clinical trial. We use randomization, as a method of allocation, primarily to reduce selection bias and imbalances between intervention arms so that the precision of the effects of the interventions is maximized.  Randomization more or less achieves these in large trials. However, in small trials, an imbalance on prognostic factors is possible between groups.

Imbalances, especially of prognostic factors, can influence estimates of treatment effects especially if the unbalanced factors are correlated or associated with study endpoints. We have seen the use of stratification as a strategy to address such imbalances.  We can stratify by factors considered important and randomize within each strata. However, we cannot have too many strata as imbalances may arise within each stratum as the number of strata increases. Ideally, the number of strata should be limited to less than 3 or 4 in a clinical trial.

Minimization is an adaptive randomization technique that allows for balancing over a large number of co-variates or strata.

A basic principle of minimization is to attempt to reduce the imbalances of prognostic factors between interventions. Minimization procedures attempt to achieve this by sequentially assigning subjects to the treatment arms in a manner that minimizes the total imbalance between arms. Minimization differs from stratification in that it considers combinations of many important prognostic factors together while stratification considers combinations of prognostic factors as mutually exclusive.

How do we minimize?

There are several methods of minimization and we shall not go into a full-fledged explanation of those here.

Briefly, we could categorize important prognostic factors and then assign them a score.

Let us look at a trial on Gestational DM as an example, using blood sugar values as an example, we can categorize uncontrolled blood sugar as yes or no, obesity as present or absent and prior nutrition education as received or not received. We can assign a score of 1 for yes or present or not received and a score of 0 for no, absent or received.

A woman who has uncontrolled blood sugar, is obese and has not previously received nutrition education now scores 1+1+1=3

A woman who has blood sugar under control, is obese and has received nutrition education scores 0+1+0=1

and so on

Let us say woman 1 had a score of 3 and is randomized to the control group (control group score=3 now)

Woman 2 has a score of 1 and is allotted to the experimental group (experimental group score=1 now)

Woman 3 has a score of 2 and she is allotted to the experimental group (experimental group score= 3 now)

When the scores are tied, the next subject is randomized (thus, woman 4 is now randomized).

This is a simple example of how the process works.

Limitations of minimization

  • This is not a truly randomization process and hence the strength of using conventional statistical tests may be questioned. However, conventional statistics tests are used.
  • We cannot predetermine the randomization for each subject, randomization is done only when the scores are tied. We could start by having “n” or 2″n” sets of patients randomly assigned and then start the minimization process.
  • Allocating patients to treatment via minimization is more complex than using simple randomization, and its degree of complexity depends on the imbalance functions and assignment probabilities chosen. Each time a subject enters the trial, the minimization schedule has to be run and the complexity increases as the number of prognostic factors increases
  • Wrongly determining the prognostic factor for a person can result in allocation to the wrong arm. If, this is detected at a later stage after enrolment, the schedule can be thrown into disarray…..we need to then consider how we deal with post randomization detection of wrong determinations. Similarly, we need to consider the effect on imbalance when subjects withdraw from the trial post randomization.

The Placebo

We can define the placebo as an inert or non-therapeutic intervention- this can be a pill, a procedure, and even a patient physician or patient health care delivery interaction.

What do we hope to achieve through the use of a placebo?

The use of a placebo is expected to help in several ways:

  • The ability to isolate the “active” or “different” part of the experimental therapy that makes it better or worse than routine care or currently offered care. This helps to differentiate the parts of the experimental therapy that work (in either direction) from the routine elements of care including the care environment, the physician patient rapport or relationship, and other aspects of the therapeutic relationship that can either improve or worsen the condition of a person.
  • The ability to “blind” or “mask” the subject and investigator to the intervention offered. Thus, the investigator will now know which subject received which intervention and the subject will not know which intervention they received. This helps to prevent potential bias in allocation to interventions and in reporting of outcomes or treatment effects.

Masking or blinding helps in several ways

  • If the clinician or the subject becomes aware that they are using the non-experimental therapy, they may find ways to use the experimental treatment outside of the trial while still being inside the trial (this can contaminate the results and lead to a bias)
  • If the clinician or the subject becomes aware that they are using the non-experimental therapy, they may provide or use other additional supplemental therapy outside the scope of the trial ( this can lead to a bias as the co-interventions may benefit or harm the subject and lead to a different result than actual)
  • When the clinician knows which intervention is provided, they may actively search and report outcomes based on their personal preferences. If they like the new experimental therapy or hope it will be better than the current options, they may actively look for signs that show the benefits of the therapy and under report adverse events. This leads to a bias in ascertainment
  • When the subject knows which intervention is provided, they may actively over or under report outcomes based on their personal preferences. They may over report benefits and under report adverse events if they want to be seen as “good, compliant” subjects.  This leads to a bias in information

The placebo effect

Can the provision of a placebo lead to a benefit? The potential benefits that a placebo can lead to are known as placebo effects. However, this term is to be used with caution. We need to consider several “scenarios” before we conclude that there is an actual placebo effect

  • We need to consider that diseases have a natural progression and it is possible that the condition improves as part of its natural course (after a particular time or a particular cut-off) without any active treatment. An example, may be the natural progress of a common cold or a flu to improvement. This can occur even for serious diseases. This can include a regression to the mean where the more serious conditions may move towards the normal range (thus a high blood pressure may over time regress to the normal range even without treatment, it may fluctuate and increase later, but there is a possibility of shifting towards the mean normal values also)
  • We need to consider if other treatments have been taken outside of the trial that have led to benefits (beneficial co-interventions)
  • We need to consider if the investigator is either over or under reporting events or benefits based on their “educated guesses” or “hunch” or “intuition” about the intervention the subject is receiving (or they may have even compromised the masking or blinding)
  • We need to consider if the subject is either over or under reporting events or benefits based on their “educated guesses” or “hunch” or “intuition” about the intervention the subject is receiving (or they may have even compromised the masking or blinding)
  • A clinical trial usually provides the subject with more intense monitoring (and sometime more politeness, attention and care as investigators work to ensure that the subject remains within the trial and does not drop out) and subjects may decide to report or over report benefits so that they can continue in the trial. This is a real possibility in trials where subjects are compensated for participation.

To really determine if there is a placebo effect, we need a 3 arm trial- an experimental therapy arm, a placebo arm and a no intervention arm.

The ethics of using a placebo

The use of a placebo is justifiable only in certain circumstances

  • If there is no established effective therapy. In this instance, the experimental group can receive the new experimental therapy and general supportive care, and the control group receives a placebo or no treatment plus general supportive care
  • If there is established effective therapy and the new treatment is viewed as a add on or supplement to the established therapy- In this instance, the experimental groupU receives the established therapy and the new treatment, and the control group receives the established therapy plus a placebo
  • If there is established effective therapy and the new treatment is viewed as superior to the established therapy- in this instance, the experimental group receives the new therapy + placebo and the control group receives the established therapy + placebo.

There are few studies where the isolated use of a placebo can be justified as ethical

Uncertainty- A (The) principle behind a randomized clinical trial

“Uncertainty” is a very important principle that drives the need for a randomized clinical trial.

Trials are started based on a guess that one intervention is better than the existing intervention (on any parameter- safety, effectiveness, efficacy, outcomes, affordability etc.). The “guess” indicates that we are uncertain if it is really true that the experimental intervention is better than the existing standard. We do a trial to reduce the “uncertainty” around this guess.

Thus, a trial is started when there is a genuine uncertainty about the relative benefits (to a group of persons or a population) of an intervention in comparison to the existing standards of care.

The trial is started when a “reasonable” number of clinicians, trialists (research methodologists) and ethics committees or institution review boards agree that the current level of evidence does not reduce the uncertainty whether an experimental intervention is better than the control.  There arises a consensus in the peer expert group that the uncertainty has to be resolved and a RCT is initiated.

Once the decision to start a trial starts, there are other levels of uncertainty that can arise.

  • An individual clinician can, in their considered judgment based on clinical experience and/or a review of existing evidence, decide that a particular intervention is not ideal for their clients. They can form a considered opinion that the experimental therapy is not ideal for their clients and prefer to use the existing standard. They would consider it unethical to offer an intervention that is not ideal in their view to their patients inside or outside a trial. It is also possible that the clinician can form a considered opinion that the experimental intervention is definitely better and would not want to withhold the intervention from any client. They would consider it unethical to withhold an intervention that, in their view, has clear benefits. In these circumstances, it would be preferable for the individual clinician to withdraw from the trial. On an idealistic plane, it could be argued that the individual clinician should cede to the “expert peer” group that has deemed the necessity for a trial. However, on a pragmatic level, it makes sense for the clinician to withdraw rather than be forced to offer an intervention they clearly do not believe in or withhold an intervention they clearly believe in. This may be considered similar to an “informed consent” for participating clinicians- they have the right to choose to participate or not (without consequences..hmm).
  • The next level of uncertainty is based around the recruitment of eligible subjects. We have the informed consent process that protects the right of the subject to make a choice, we have the inclusion and exclusion criteria to determine who is eligible for enrolment. A critical step (not sure how well this is enforced) is the determination of the “uncertainty” for both the clinician and the subject. “Is the clinician or investigator “uncertain” how the experimental intervention fares in comparison to the existing standard? Are there special characteristics for the patient where the clinician feels the experimental intervention may offer clear and marked benefits or lead to clear and marked adverse events?  Can the clinician say with conviction “I really am not sure how this intervention will work for you compared to the existing standard”?

Do not enrol the subject into the trial if either the subject or the clinician believe that one or the other intervention is clearly beneficial (or harmful).  

Enrol a subject into a trial ONLY if both the subject and the clinician (AFTER A MEANINGFUL DISCUSSION) remain uncertain about the relative effectiveness of the interventions.

Written by

Leave a Reply

Your email address will not be published.

The Current Informed Consent Process & Missed/Misinterpreted Findings

Selecting statistical tests for your quantitative research