experimental placebo group

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Experimental Group in Psychology Experiments

In a randomized and controlled psychology experiment , the researchers are examining the impact of an experimental condition on a group of participants (does the independent variable 'X' cause a change in the dependent variable 'Y'?). To determine cause and effect, there must be at least two groups to compare, the experimental group and the control group.

The participants who are in the experimental condition are those who receive the treatment or intervention of interest. The data from their outcomes are collected and compared to the data from a group that did not receive the experimental treatment. The control group may have received no treatment at all, or they may have received a placebo treatment or the standard treatment in current practice.

Comparing the experimental group to the control group allows researchers to see how much of an impact the intervention had on the participants.

A Closer Look at Experimental Groups

Imagine that you want to do an experiment to determine if listening to music while working out can lead to greater weight loss. After getting together a group of participants, you randomly assign them to one of three groups. One group listens to upbeat music while working out, one group listens to relaxing music, and the third group listens to no music at all. All of the participants work out for the same amount of time and the same number of days each week.

In this experiment, the group of participants listening to no music while working out is the control group. They serve as a baseline with which to compare the performance of the other two groups. The other two groups in the experiment are the experimental groups.   They each receive some level of the independent variable, which in this case is listening to music while working out.

In this experiment, you find that the participants who listened to upbeat music experienced the greatest weight loss result, largely because those who listened to this type of music exercised with greater intensity than those in the other two groups. By comparing the results from your experimental groups with the results of the control group, you can more clearly see the impact of the independent variable.  

Some Things to Know

When it comes to using experimental groups in a psychology experiment, there are a few important things to know:

• In order to determine the impact of an independent variable, it is important to have at least two different treatment conditions. This usually involves using a control group that receives no treatment against an experimental group that receives the treatment. However, there can also be a number of different experimental groups in the same experiment.
• Care must be taken when assigning participants to groups. So how do researchers determine who is in the control group and who is in the experimental group? In an ideal situation, the researchers would use random assignment to place participants in groups. In random assignment, each individual stands an equal shot at being assigned to either group. Participants might be randomly assigned using methods such as a coin flip or a number draw. By using random assignment, researchers can help ensure that the groups are not unfairly stacked with people who share characteristics that might unfairly skew the results.
• Variables must be well-defined. Before you begin manipulating things in an experiment, you need to have very clear operational definitions in place. These definitions clearly explain what your variables are, including exactly how you are manipulating the independent variable and exactly how you are measuring the outcomes.

A Word From Verywell

Experiments play an important role in the research process and allow psychologists to investigate cause-and-effect relationships between different variables. Having one or more experimental groups allows researchers to vary different levels or types of the experimental variable and then compare the effects of these changes against a control group. The goal of this experimental manipulation is to gain a better understanding of the different factors that may have an impact on how people think, feel, and act.

Byrd-Bredbenner C, Wu F, Spaccarotella K, Quick V, Martin-Biggers J, Zhang Y. Systematic review of control groups in nutrition education intervention research . Int J Behav Nutr Phys Act. 2017;14(1):91. doi:10.1186/s12966-017-0546-3

Steingrimsdottir HS, Arntzen E. On the utility of within-participant research design when working with patients with neurocognitive disorders . Clin Interv Aging. 2015;10:1189-1200. doi:10.2147/CIA.S81868

Oberste M, Hartig P, Bloch W, et al. Control group paradigms in studies investigating acute effects of exercise on cognitive performance—An experiment on expectation-driven placebo effects . Front Hum Neurosci. 2017;11:600. doi:10.3389/fnhum.2017.00600

Kim H. Statistical notes for clinical researchers: Analysis of covariance (ANCOVA) . Restor Dent Endod . 2018;43(4):e43. doi:10.5395/rde.2018.43.e43

Bate S, Karp NA. A common control group — Optimising the experiment design to maximise sensitivity . PLoS ONE. 2014;9(12):e114872. doi:10.1371/journal.pone.0114872

Myers A, Hansen C. Experimental Psychology . 7th Ed. Cengage Learning; 2012.

By Kendra Cherry, MSEd Kendra Cherry, MS, is a psychosocial rehabilitation specialist, psychology educator, and author of the "Everything Psychology Book."

The Difference Between Control Group and Experimental Group

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In an experiment , data from an experimental group is compared with data from a control group. These two groups should be identical in every respect except one: the difference between a control group and an experimental group is that the independent variable is changed for the experimental group, but is held constant in the control group.

Key Takeaways: Control vs. Experimental Group

• The control group and experimental group are compared against each other in an experiment. The only difference between the two groups is that the independent variable is changed in the experimental group. The independent variable is "controlled", or held constant, in the control group.
• A single experiment may include multiple experimental groups, which may all be compared against the control group.
• The purpose of having a control is to rule out other factors which may influence the results of an experiment. Not all experiments include a control group, but those that do are called "controlled experiments."
• A placebo may also be used in an experiment. A placebo isn't a substitute for a control group because subjects exposed to a placebo may experience effects from the belief they are being tested; this itself is known as the placebo effect.

What Are Is an Experimental Group in Experiment Design?

An experimental group is a test sample or the group that receives an experimental procedure. This group is exposed to changes in the independent variable being tested. The values of the independent variable and the impact on the dependent variable are recorded. An experiment may include multiple experimental groups at one time.

A control group is a group separated from the rest of the experiment such that the independent variable being tested cannot influence the results. This isolates the independent variable's effects on the experiment and can help rule out alternative explanations of the experimental results.

While all experiments have an experimental group, not all experiments require a control group. Controls are extremely useful where the experimental conditions are complex and difficult to isolate. Experiments that use control groups are called controlled experiments .

A Simple Example of a Controlled Experiment

A simple example of a controlled experiment may be used to determine whether or not plants need to be watered to live. The control group would be plants that are not watered. The experimental group would consist of plants that receive water. A clever scientist would wonder whether too much watering might kill the plants and would set up several experimental groups, each receiving a different amount of water.

Sometimes setting up a controlled experiment can be confusing. For example, a scientist may wonder whether or not a species of bacteria needs oxygen in order to live. To test this, cultures of bacteria may be left in the air, while other cultures are placed in a sealed container of nitrogen (the most common component of air) or deoxygenated air (which likely contained extra carbon dioxide). Which container is the control? Which is the experimental group?

Control Groups and Placebos

The most common type of control group is one held at ordinary conditions so it doesn't experience a changing variable. For example, If you want to explore the effect of salt on plant growth, the control group would be a set of plants not exposed to salt, while the experimental group would receive the salt treatment. If you want to test whether the duration of light exposure affects fish reproduction, the control group would be exposed to a "normal" number of hours of light, while the duration would change for the experimental group.

Experiments involving human subjects can be much more complex. If you're testing whether a drug is effective or not, for example, members of a control group may expect they will not be unaffected. To prevent skewing the results, a placebo may be used. A placebo is a substance that doesn't contain an active therapeutic agent. If a control group takes a placebo, participants don't know whether they are being treated or not, so they have the same expectations as members of the experimental group.

However, there is also the placebo effect to consider. Here, the recipient of the placebo experiences an effect or improvement because she believes there should be an effect. Another concern with a placebo is that it's not always easy to formulate one that truly free of active ingredients. For example, if a sugar pill is given as a placebo, there's a chance the sugar will affect the outcome of the experiment.

Positive and Negative Controls

Positive and negative controls are two other types of control groups:

• Positive control groups are control groups in which the conditions guarantee a positive result. Positive control groups are effective to show the experiment is functioning as planned.
• Negative control groups are control groups in which conditions produce a negative outcome. Negative control groups help identify outside influences which may be present that were not unaccounted for, such as contaminants.
• Bailey, R. A. (2008). Design of Comparative Experiments . Cambridge University Press. ISBN 978-0-521-68357-9.
• Chaplin, S. (2006). "The placebo response: an important part of treatment". Prescriber : 16–22. doi: 10.1002/psb.344
• Hinkelmann, Klaus; Kempthorne, Oscar (2008). Design and Analysis of Experiments, Volume I: Introduction to Experimental Design (2nd ed.). Wiley. ISBN 978-0-471-72756-9.
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• What Is the Placebo Effect? | Definition & Examples

What Is the Placebo Effect? | Definition & Examples

Published on October 16, 2022 by Kassiani Nikolopoulou . Revised on March 6, 2023.

The placebo effect is a phenomenon where people report real improvement after taking a fake or nonexistent treatment, called a placebo . Because the placebo can’t actually cure any condition, any beneficial effects reported are due to a person’s belief or expectation that their condition is being treated.

The placebo effect is often observed in experimental designs where participants are randomly assigned to either a control or treatment group. 

Table of contents

What is a placebo, what is the definition of placebo effect, how does the placebo effect work, placebo effect examples, downside of the placebo effect, other types of research bias, frequently asked questions about the placebo effect.

A placebo can be a sugar pill, a salt water injection, or even a fake surgical procedure. In other words, a placebo has no therapeutic properties . Placebos are often used in medical research and clinical trials to help scientists evaluate the effects of new medications.

In these clinical trials, participants are randomly assigned to either the placebo or the experimental medication. Crucially, they are not aware of which treatment they receive. The results of the two groups are compared, to see whether they differ.

In double-blind studies , researchers also don’t know who received the actual treatment or the placebo. This is to prevent them from conveying demand characteristics to participants that could influence the study’s results. This is preferred over single-blind studies, where participants do not know which group they have been placed in, but researchers do.

Placebos may help relieve symptoms like pain, fatigue, or stress-related insomnia, but they don’t actually treat a condition or cure a disease. Note that due to ethical considerations , placebos are not always used in clinical trials. For example, as it would be unethical to leave terminal cancer patients untreated, placebos aren’t used in these types of studies.

For some people, just the idea that they are taking medication makes them feel better. This occurs even if the medication is actually just a placebo. This phenomenon is known as the placebo effect . In other words, the perception of feeling better is triggered by the person’s belief in the benefit of the treatment.

When studying a new treatment, researchers must demonstrate that it is more effective than can just be explained by the placebo effect. To do so, they compare the results from those taking the new treatment with those from the placebo. In order to accurately compare the two groups, participants in clinical trials must not know whether they received the treatment or the placebo. If the two groups have the same reaction, the effectiveness of the new treatment is not supported.

Although the exact reasons for the positive effects of placebos are still being researched, a number of factors contribute to the phenomenon. These include:

• A person’s expectations or beliefs that they will get better . People who are motivated and expect their treatment to work are more likely to experience the placebo effect.
• The feeling of receiving attention and care due to participation in the study. This may reduce stress levels and trigger the body’s own pain-relieving chemicals.
• Classical conditioning , or the association people build over the years between a certain action, such as pill-taking, and positive results.
• A trusting relationship between doctors and patients or researchers and study participants from the sample . Listening to an expert you trust talk enthusiastically about a treatment can impact how you respond to it.

However, researchers do not attribute the placebo effect exclusively to psychology. A few other possible explanations include:

• Regression to the mean: When people first visit a doctor or start on a clinical trial, their symptoms might be particularly bad. But in the natural course of an illness, symptoms may subside on their own.
• Confirmation bias : Feelings of hopefulness about a new treatment may lead people to pay more attention to signs that they’re getting better and less attention to signs that they’re getting worse.

The placebo effect illustrates how the mind can trigger changes in the body.

After participants take the pill, their blood pressure and pulse rate increases, and their reaction speeds are improved.

However, when the same people are given the same pill and told it will help them relax and sleep, they report experiencing relaxation instead.

The placebo effect can also explain the popularity of non-FDA-approved products.

Evidence from published studies show that it takes extremely high doses for CBD to be effective. Documented benefits of CBD in placebo-control trials require anywhere from hundreds to thousands of milligrams per day. This is the equivalent of taking almost an entire bottle each day, depending on the concentration.

Most people take 15 milligrams or less per day, far less than what the studies deem an effective dose. The placebo effect seems to play a role here: the expectation is so high that people start to believe it’s working.

The response of people assigned to the placebo control group may not always be positive. They may experience what is called a “nocebo effect,” or a negative outcome, when taking a placebo. The same explanation applies here. If you expect a negative outcome, it’s more likely you’ll have a negative outcome.

For example, in a clinical trial, participants who are given a placebo but are told what side effects the “treatment” may cause. They may have the same side effects as the participants who are given the active treatment, only because they expect them to occur.

Cognitive bias

• Confirmation bias
• Baader–Meinhof phenomenon
• Availability heuristic
• Halo effect
• Framing effect
• Optimism bias
• Negativity bias
• Affect heuristic
• Representativeness heuristic
• Anchoring heuristic
• Primacy bias

Selection bias

• Sampling bias
• Ascertainment bias
• Attrition bias
• Self-selection bias
• Survivorship bias
• Nonresponse bias
• Undercoverage bias
• Hawthorne effect
• Observer bias
• Omitted variable bias
• Publication bias
• Pygmalion effect
• Recall bias
• Social desirability bias
• Placebo effect
• Actor-observer bias
• Ceiling effect
• Ecological fallacy
• Affinity bias

Although there is no definite answer to what causes the placebo effect , researchers propose a number of explanations such as the power of suggestion, doctor-patient interaction, classical conditioning, etc.

Placebos are used in medical research for new medication or therapies, called clinical trials. In these trials some people are given a placebo, while others are given the new medication being tested.

The purpose is to determine how effective the new medication is: if it benefits people beyond a predefined threshold as compared to the placebo, it’s considered effective and not the result of a placebo effect .

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1.4.4 - Control and Placebo Groups

A  control group  is an experimental condition that does not receive the actual treatment and may serve as a baseline. A control group may receive a placebo or they may receive no treatment at all. A  placebo  is something that appears to the participants to be an active treatment, but does not actually contain the active treatment. For example, a placebo pill is a sugar pill that participants may take not knowing that it does not contain any active medicine. This can lead to a psychological phenomena called the placebo effect  which occurs when participants who are given a placebo treatment experience a change even though they are not receiving any active treatment. Researchers use placebos in the control group to determine if any differences between groups are due to the active medicine or the participants' perceptions (the placebo effect).

Example: Vitamin B Energy Study

Researchers want to know if adults who consume a drink that is high in vitamin B-12 have increased energy. They obtain a representative sample of adults. All participants are given a drink that they are told to consume every morning. They are not told what is in the drink. Half are given a drink that is high in vitamin B-12 while the other half are given a drink that tastes the same but contains no vitamin B-12.

The participants who received the drink with no vitamin B-12 are the placebo group . The purpose of the placebo group in this study is to make the two groups equivalent except for the presence of the vitamin B-12. By comparing these two groups, the researchers will be able to determine what impact the vitamin B-12 had on the response variable. We could also say that this served as a  control group  because this group did not receive any active ingredients. 

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Placebo Effect – What It Is and How It Works

The placebo effect is the phenomenon where a subject experiences an effect from an inactive substance or fake treatment, which is called a placebo . While not all people experience the placebo effect (certainly not in all situations), there are genuine therapeutic effects of placebos. Here is a look at what the placebo effect is, why it occurs, and how scientists and health professionals use it.

• A placebo is a fake treatment, which can have genuine therapeutic value, called the placebo effect.
• Examples of placebos include sugar pills and saline solution injections.
• The placebo effect helps providing relief from depression, pain, and certain other conditions.
• Overall, the placebo effect occurs because any treatment (real or a placebo) affects the brain, which responds to the stimulus and produces a physiological effect.

Placebo vs Placebo Effect

The placebo effect is a therapeutic benefit or apparent side effect from a placebo. A placebo, in turn, is a substance or treatment that has no effect. Alternatively, it is a treatment with the exact composition of inactive ingredients or the same steps as the therapy, minus the active substance or procedure.

Examples of placebos include sugar pills, consumable liquids or solids, saline injections, and fake surgeries.

The Nocebo Effect

Sometimes the placebo effect refers to any response to a fake treatment. However, other scientists refer to a therapeutic or beneficial response as the placebo effect and side effects or a negative response as the nocebo effect (negative placebo). The nocebo effect also includes withdrawal symptoms some patients experience after discontinuing a placebo treatment.

Uses of Placebos

The primary use of a placebo is in scientific research and drug testing. A researcher administers the placebo to a control group , while the experimental group receives the treatment. Assuming the placebo is identical to the treatment in every respect except the active ingredient or treatment, this type of experiment identifies the efficacy of the treatment with a high degree of confidence. Also, using a placebo makes double blind experiments possible.

However, when you compare the outcomes for an experimental group, placebo group, and a control group that receives no treatment whatsoever, then the placebo effect becomes apparent. This type of study also reveals “inactive ingredients” that aren’t actually inactive. The placebo effect does not influence the outcomes of all studies, but it is a major factor in others.

Situations Where Placebos Work

So, knowing that the placebo effect is a real phenomenon, scientists and medical professionals studied the effectiveness of placebos. In some situations, a placebo is an effective treatment, even when people know they are taking a placebo. Placebos have an effect on:

• Irritable bowel syndrome
• Sleep disorders

Studies indicate some people taking a placebo for a stimulant experience increased heart rate and blood pressure, while those taking a placebo for a depressant experience the opposite effects.

How the Placebo Effect Works

There is no single definitive mechanism for how the placebo effect works. Multiple factors likely play a role:

• Expectation : Basically, what we believe we will experience from a treatment plays a part in the actual effect. So, if you think an injection will hurt, it probably will. Or, if you think a pill (real or placebo) helps a condition, then it likely does. Even if you know a treatment is a placebo, receiving care from a health professional aids in a positive response.
• Conditioning : Conditioning is a learned response or association between two events. For example, in one study, rats drank a saccharin-sweetened beverage containing the immunosuppressant cyclophosphamide. After three days of conditioning, rats given the saccharin beverage minus the cyclophosphamide still displayed suppressed immune responses.
• Genetics : Some subjects are genetically predisposed to respond to placebos. For example, in one study, people carrying a gene coding for higher levels of the neurotransmitter dopamine were more likely to experience the placebo effect than those with a gene for lower dopamine production.

Studies indicate that the brain controls a variety of responses that manifest as the placebo effect. Physiological processes subject to placebos include pain response, depression, insulin secretion, immunosuppression, symptoms of Parkinson’s disease, and serum iron levels. Brain imaging shows a placebo for pain relief activates several regions of the nervous system, including the spinal cord, amygdala, nucleus accumbens, and anterior cingulate, insular, orbitofrontal, and prefrontal cortices in the brain.

• Ader, R.; Cohen, N. (1975). “Behaviorally conditioned immunosuppression”. Psychosomatic Medicine . 37 (4): 333–40. doi: 10.1097/00006842-197507000-00007
• Eippert, F.; Bingel, U.; Schoell, E.D.; et al. (2009). “Activation of the opioidergic descending pain control system underlies placebo analgesia”. Neuron . 63 (4):533-543. doi: 10.1016/j.neuron.2009.07.014
• Gross, Liza (2017). “Putting placebos to the test”. PLOS Biology . 15 (2): e2001998. doi: 10.1371/journal.pbio.2001998
• Häuser, W.; Hansen, E.; Enck, P. (June). “Nocebo phenomena in medicine: their relevance in everyday clinical practice”. Deutsches Ärzteblatt International . 109 (26): 459–65. doi: 10.3238/arztebl.2012.0459
• Khan, A.; Redding, N.; Brown, W.A. (2008). “The persistence of the placebo response in antidepressant clinical trials”. Journal of Psychiatric Research . 42 (10): 791–6. doi: 10.1016/j.jpsychires.2007.10.004
• Price, D.D.; Finniss, D.G.; Benedetti, F. (2008). “A comprehensive review of the placebo effect: recent advances and current thought”. Annual Review of Psychology . 59 (1): 565–90. doi: 10.1146/annurev.psych.59.113006.095941

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Clinical Research: Benefits, Risks, and Safety

On this page:

What are the potential benefits of participating in clinical research?

What are the potential risks of participating in clinical research, will i always get the experimental treatment in a clinical trial, how is the safety of clinical research participants protected.

If you’re interested in volunteering for clinical research, you may wonder: What makes a study a good fit for me? How do I know it’s safe? Clinical research involves studying health and illness in people through observational studies or clinical trials . Participating in a trial or study has many potential benefits and also some possible risks. Learn about the benefits and risks of participating in clinical research and how your safety is protected.

There are many possible benefits of being part of clinical research, including:

• You may have the chance to help scientists better understand your disease or condition and to advance treatments and ways to prevent it in the future.
• You may feel like you’re playing a more active role in your health.
• You may learn more about your disease or condition.
• You may be able to get information about support groups and resources.

In addition, some people participate in clinical trials because they hope to gain access to a potential new treatment for a disease before it is widely available.

Clinical trials and studies do come with some possible risks, including:

• The research may involve tests that pose a risk to participants. For example, certain physical tests may increase the chance of falling, and X-rays may cause a small increase in the risk of developing cancer.
• Participating in a study could also be inconvenient for you. For example, you may be required to have additional or longer medical appointments, more procedures, complex medication instructions, or hospital stays.

Additional risks of participating in clinical trials may include:

• For those who receive the experimental treatment, it may be uncomfortable or cause side effects (which can range from mild to serious).
• The experimental treatment might not work, or it may not be better than the standard treatment.
• For trials testing a new treatment, such as a new medication or device, you may end up not being part of the group that gets the experimental treatment. Instead, you may be assigned to the control (or comparison) group. In some studies, the control group receives a placebo, which is given in the same way as the treatment but has no effect.

Participant confidentiality is a concern in any kind of research. People other than the researchers, such as the study sponsors or experts who monitor safety, may be able to access medical information related to the study. Safeguards are in place to ensure that researchers tell potential participants what information could be shared and how their privacy will be protected before they consent to participate in research.

The study coordinators will provide detailed information and answer questions about the risks and benefits of participating in a particular study. Having this information can help you make an informed decision about whether to participate.

Clinical trial volunteers do not always get the treatment being tested. The gold standard for testing interventions in people is called a randomized controlled trial. Randomized means that volunteers are randomly assigned — chosen by chance — to receive either the experimental intervention (the test group) or a placebo or the current standard care (the control or comparison group). Then, researchers compare the effects in each group to determine whether the new treatment works.

When you enroll in a clinical trial, you may be assigned to the test group or to the control group. While participants in the control group do not receive the experimental treatment, these volunteers are just as important as those in the test group. Without the control group, scientists cannot be sure whether an experimental treatment is better than the standard or no treatment.

In many cases, you won’t know until the end of the trial whether you are in the test group or the control group. That’s because knowing the group assignment might influence the results of the trial. Studies are often “blinded” (or “masked”) to prevent this accidental bias. In a single-blind study, you are not told whether you are in the test group or the control group, but the research team knows. In a double-blind study, neither you nor the research team knows what group you are in until the trial is over. If medically necessary, however, it is always possible to find out which group you are in.

What is a placebo?

Whenever possible, clinical trials compare a new treatment for a specific condition to the standard treatment for that condition. When there is no standard treatment available, scientists may compare the new treatment to a placebo, which looks like the drug or treatment being tested but isn’t meant to actually change anything in your body. A pill that doesn’t contain any medicine is one example.

A trial that uses a placebo is described as a “placebo-controlled trial.” In this type of study, the test group receives the experimental treatment, and the control group receives the placebo.

Placebos are not used if an effective treatment is already available or if you would be put at risk by not having effective therapy. You will be told if placebos are used in the study before entering a trial as part of the process of informed consent.

What happens if a clinical trial ends early?

Most clinical trials run as planned from beginning to end. However, sometimes researchers end trials early. Clinical trials may be paused or stopped for a number of reasons:

• There is clear evidence that one intervention is more effective than another. When this happens, the trial may be stopped so that the new treatment can be made available to other people as soon as possible.
• The trial shows that the treatment doesn’t work or causes unexpected and serious side effects.
• The researchers can’t enroll enough people in the trial to provide meaningful results.

Even when a clinical trial ends early, it can still provide researchers with valuable information. For example, scientists may gain insights about how to best design and conduct clinical trials in a specific research area. In some cases, health information collected during a trial can lead to new potential therapies that researchers can test in the future.

Based on many years of experience and learning from past mistakes, strict rules are in place to keep participants safe . Today, every clinical investigator in the United States is required to monitor and make sure that every participant is safe. These safeguards are an essential part of the research.

Each clinical study follows a careful study plan, called a protocol, which describes what the researchers will do. The principal investigator, or head researcher, is responsible for ensuring the protocol is followed.

Safeguards to protect clinical research volunteers include Institutional Review Boards, informed consent, Data and Safety Monitoring Boards, and Observational Study Monitoring Boards.

• Most clinical studies in the U.S. must be approved by an Institutional Review Board (IRB) . The IRB is made up of doctors, scientists, and members of the general public who ensure that the study participants are not exposed to unnecessary risks. The people on the IRB regularly review the study and its results. They make sure that risks (or potential harm) to participants do not outweigh the potential benefits of the study.
• Informed consent also helps protect participants. Informed consent is the process by which you learn the key facts about a study before deciding whether to participate. Members of the research team explain the research before you start and throughout the study. They provide an informed consent document, which includes details about the study, such as its purpose, how long it will last, required procedures, and who to contact. The informed consent document also explains risks and potential benefits. You are free to ask questions, request more information, or withdraw from the study at any time.

Clinical trials and studies also have committees that monitor the safety of the research as it occurs.

• Clinical trials that test an intervention are closely supervised by a Data and Safety Monitoring Board . The board is made up of experts who review the results of the study as it progresses. If they determine that the experimental treatment is not working or is harming participants, they can stop the trial early.
• Observational Study Monitoring Boards monitor the safety of observational studies with large or vulnerable populations, or risks associated with tests or standard of care.

Several historical incidents have caused mistrust in clinical research. These events also led to the creation of laws that provide clinical research participants with multiple levels of protection.

One example is the U.S. Public Health Service Syphilis Study at Tuskegee , which was conducted between 1932 and 1972. In this study, researchers wanted to determine the effects of untreated syphilis. They did not explain the study’s risks or obtain informed consent from the participants, all of whom were Black men. They also did not offer the study participants penicillin when it became widely available in the mid-1940s, causing preventable illness and suffering. After news of the study leaked in 1972, it led to sweeping changes in standard research practices and guidelines to protect human research participants. Today, IRBs are responsible for reviewing all studies involving humans to ensure they meet these guidelines and for reporting any study plan that breaks the rules.

After obtaining all the information, you can make an informed decision about whether or not to participate in a clinical trial or study. If you decide to volunteer for clinical research, you will be given an informed consent form to sign. By signing the form, you show that you understand the details and want to be part of the research. However, the informed consent form is not a contract. You may leave the study at any time and for any reason.

Where can I find a clinical trial or study?

Looking for clinical research related to aging and age-related health conditions? There are many ways to find a trial or study. Talk to your health care provider and use online resources to:

• Search for a clinical trial or study .
• Look for clinical trials on Alzheimer’s disease, other dementias, and caregiving .
• Find a registry for a particular diagnosis or condition .
• Explore clinical trials and studies funded by NIA .

To learn more about a particular trial or study, you or your doctor can contact the research staff and ask questions. You can usually find contact information in the study description.

You may also be interested in

• Getting more information about clinical trials and studies
• Downloading and sharing an infographic with the benefits of participating in clinical research
• Learning about participating in Alzheimer's disease research

For more information about clinical research

Clinical Research Trials and You National Institutes of Health www.nih.gov/health-information/nih-clinical-research-trials-you

ClinicalTrials.gov www.clinicaltrials.gov 

U.S. Food and Drug Administration 888-463-6332 [email protected] www.fda.gov

This content is provided by the NIH National Institute on Aging (NIA). NIA scientists and other experts review this content to ensure it is accurate and up to date.

Content reviewed: May 18, 2023

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How Treatment Groups, Control Groups, Placebos, and Blind Experiments Are Used in Statistics

Statistics for dummies.

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Statistical studies often involve several kinds of experiments: treatment groups, control groups, placebos, and blind and double-blind tests. An experiment is a study that imposes a treatment (or control) to the subjects (participants), controls their environment (for example, restricting their diets, giving them certain dosage levels of a drug or placebo, or asking them to stay awake for a prescribed period of time), and records the responses.

The purpose of most experiments is to pinpoint a cause-and-effect relationship between two factors (such as alcohol consumption and impaired vision; or dosage level of a drug and intensity of side effects). Here are some typical questions that experiments try to answer:

Does taking zinc help reduce the duration of a cold? Some studies show that it does.

Does the shape and position of your pillow affect how well you sleep at night? The Emory Spine Center in Atlanta says yes.

Does shoe heel height affect foot comfort? A study done at UCLA says up to one-inch heels are better than flat soles.

Treatment-group versus control-group tests

Most experiments try to determine whether some type of experimental treatment (or important factor) has a significant effect on an outcome. For example, does zinc help to reduce the length of a cold? Subjects who are chosen to participate in the experiment are typically divided into two groups: a treatment group and a control group. (More than one treatment group is possible.)

The treatment group consists of participants who receive the experimental treatment whose effect is being studied (in this case, zinc tablets).

The control group consists of participants who do not receive the experimental treatment being studied. Instead, they get a placebo (a fake treatment; for example, a sugar pill); a standard, nonexperimental treatment (such as vitamin C, in the zinc study); or no treatment at all, depending on the situation.

In the end, the responses of those in the treatment group are compared with the responses from the control group to look for differences that are statistically significant (unlikely to have occurred just by chance).

Placebo tests

A placebo is a fake treatment, such as a sugar pill. Placebos are given to the control group to account for a psychological phenomenon called the placebo effect, in which patients receiving a fake treatment still report having a response, as if it were the real treatment. For example, after taking a sugar pill a patient experiencing the placebo effect might say, “Yes, I feel better already,” or “Wow, I am starting to feel a bit dizzy.” By measuring the placebo effect in the control group, you can tease out what portion of the reports from the treatment group were due to a real physical effect and what portion were likely due to the placebo effect. (Experimenters assume that the placebo effect affects both the treatment and control groups similarly.)

Blind and double-blind tests

A blind experiment is one in which the subjects who are participating in the study are not aware of whether they’re in the treatment group or the control group. In the zinc example, the vitamin C tablets and the zinc tablets would be made to look exactly alike and patients would not be told which type of pill they were taking. A blind experiment attempts to control for bias on the part of the participants and to ensure that a placebo effect will not affect only the treatment group. (If the example study was not blind, those not taking zinc may not bother to take their pills or may believe they won’t get better because they know they’re not taking the good stuff.)

A double-blind experiment controls for potential bias on the part of both the patients and the researchers. Neither the patients nor the researchers collecting the data know which subjects received the treatment and which didn’t. So who does know what’s going on as far as who gets what treatment? Typically a third party (someone not otherwise involved in the experiment) puts together the pieces independently, and only he knows which subjects received the treatment and which did not. A double-blind study is best, because even though researchers may claim to be unbiased, they often have a special interest in the results — otherwise they wouldn’t be doing the study!

About This Article

This article is from the book:.

• Statistics For Dummies ,

About the book author:

Deborah J. Rumsey , PhD, is an Auxiliary Professor and Statistics Education Specialist at The Ohio State University. She is the author of Statistics For Dummies, Statistics II For Dummies, Statistics Workbook For Dummies, and Probability For Dummies.

This article can be found in the category:

• Statistics ,
• Statistics For Dummies Cheat Sheet
• Checking Out Statistical Confidence Interval Critical Values
• Handling Statistical Hypothesis Tests
• Statistically Figuring Sample Size
• Surveying Statistical Confidence Intervals
• View All Articles From Book

Double-Blind Experimental Study And Procedure Explained

Julia Simkus

Editor at Simply Psychology

BA (Hons) Psychology, Princeton University

Julia Simkus is a graduate of Princeton University with a Bachelor of Arts in Psychology. She is currently studying for a Master's Degree in Counseling for Mental Health and Wellness in September 2023. Julia's research has been published in peer reviewed journals.

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Saul McLeod, PhD

Editor-in-Chief for Simply Psychology

BSc (Hons) Psychology, MRes, PhD, University of Manchester

Saul McLeod, PhD., is a qualified psychology teacher with over 18 years of experience in further and higher education. He has been published in peer-reviewed journals, including the Journal of Clinical Psychology.

Olivia Guy-Evans, MSc

Associate Editor for Simply Psychology

BSc (Hons) Psychology, MSc Psychology of Education

Olivia Guy-Evans is a writer and associate editor for Simply Psychology. She has previously worked in healthcare and educational sectors.

On This Page:

What is a Blinded Study?

• Binding, or masking, refers to withholding information regarding treatment allocation from one or more participants in a clinical research study, typically in randomized control trials .
• A blinded study prevents the participants from knowing about their treatment to avoid bias in the research. Any information that can influence the subjects is withheld until the completion of the research.
• Blinding can be imposed on any participant in an experiment, including researchers, data collectors, evaluators, technicians, and data analysts. 
• Good blinding can eliminate experimental biases arising from the subjects’ expectations, observer bias, confirmation bias, researcher bias, observer’s effect on the participants, and other biases that may occur in a research test.
• Studies may use single-, double- or triple-blinding. A trial that is not blinded is called an open trial.

Double-Blind Studies

Double-blind studies are those in which neither the participants nor the experimenters know who is receiving a particular treatment.

Double blinding prevents bias in research results, specifically due to demand characteristics or the placebo effect.

Demand characteristics are subtle cues from researchers that can inform the participants of what the experimenter expects to find or how participants are expected to behave.

If participants know which group they are assigned to, they might change their behavior in a way that would influence the results. Similarly, if a researcher knows which group a participant is assigned to, they might act in a way that reveals the assignment or influences the results.

Double-blinding attempts to prevent these risks, ensuring that any difference(s) between the groups can be attributed to the treatment. 

On the other hand, single-blind studies are those in which the experimenters are aware of which participants are receiving the treatment while the participants are unaware.

Single-blind studies are beneficial because they reduce the risk of errors due to subject expectations. However, single-blind studies do not prevent observer bias, confirmation bias , or bias due to demand characteristics.

Because the experiments are aware of which participants are receiving which treatments, they are more likely to reveal subtle clues that can accidentally influence the research outcome.

Double-blind studies are considered the gold standard in research because they help to control for experimental biases arising from the subjects’ expectations and experimenter biases that emerge when the researchers unknowingly influence how the subjects respond or how the data is collected.

Using the double-blind method improves the credibility and validity of a study .

Example Double-Blind Studies

Rostock and Huber (2014) used a randomized, placebo-controlled, double-blind study to investigate the immunological effects of mistletoe extract. However, their study showed that double-blinding is impossible when the investigated therapy has obvious side effects. 

Using a double-blind study, Kobak et al. (2005) found that S t John’s wort ( Hypericum perforatum ) is not an efficacious treatment for anxiety disorder, specifically OCD.

Using the Yale–Brown Obsessive–Compulsive Scale (Y-BOCS), they found that the mean change with St John’s wort was not significantly different from the mean change found with placebo. 

Cakir et al. (2014) conducted a randomized, controlled, and double-blind study to test the efficacy of therapeutic ultrasound for managing knee osteoarthritis.

They found that all assessment parameters significantly improved in all groups without a significant difference, suggesting that therapeutic ultrasound provided no additional benefit in improving pain and functions in addition to exercise training.

Using a randomized double-blind study, Papachristofilou et al. (2021) found that whole-lung LDRT failed to improve clinical outcomes in critically ill patients admitted to the intensive care unit requiring mechanical ventilation for COVID-19 pneumonia.

Double-Blinding Procedure

Double blinding is typically used in clinical research studies or clinical trials to test the safety and efficacy of various biomedical and behavioral interventions.

In such studies, researchers tend to use a placebo. A placebo is an inactive substance, typically a sugar pill, that is designed to look like the drug or treatment being tested but has no effect on the individual taking it. 

The placebo pill was given to the participants who were randomly assigned to the control group. This group serves as a baseline to determine if exposure to the treatment had any significant effects.

Those randomly assigned to the experimental group are given the actual treatment in question. Data is collected from both groups and then compared to determine if the treatment had any impact on the dependent variable.

All participants in the study will take a pill or receive a treatment, but only some of them will receive the real treatment under investigation while the rest of the subjects will receive a placebo. 

With double blinding, neither the participants nor the experimenters will have any idea who receives the real drug and who receives the placebo. 

For Example

A common example of double-blinding is clinical studies that are conducted to test new drugs.

In these studies, researchers will use random assignment to allocate patients into one of three groups: the treatment/experimental group (which receives the drug), the placebo group (which receives an inactive substance that looks identical to the treatment but has no drug in it), and the control group (which receives no treatment).

Both participants and researchers are kept unaware of which participants are allocated to which of the three groups.

The effects of the drug are measured by recording any symptoms noticed in the patients.

Once the study is unblinded, and the researchers and participants are made aware of who is in which group, the data can be analyzed to determine whether the drug had effects that were not seen in the placebo or control group, but only in the experimental group. 

Double-blind studies can also be beneficial in nonmedical interventions, such as psychotherapIes.

Reduces risk of bias

Double-blinding can eliminate, or significantly reduce, both observer bias and participant biases.

Because both the researcher and the subjects are unaware of the treatment assignments, it is difficult for their expectations or behaviors to influence the study.

Results can be duplicated

The results of a double-blind study can be duplicated, enabling other researchers to follow the same processes, apply the same test item, and compare their results with the control group.

If the results are similar, then it adds more validity to the ability of a medication or treatment to provide benefits. 

It tests for three groups

Double-blind studies usually involve three groups of subjects: the treatment group, the placebo group, and the control group.

The treatment and placebo groups are both given the test item, although the researcher does not know which group is getting real treatment or placebo treatment.

The control group doesn’t receive anything because it serves as the baseline against which the other two groups are compared.

This is an advantage because if subjects in the placebo group improved more than the subjects in the control group, then researchers can conclude that the treatment administered worked.

Applicable across multiple industries

Double-blind studies can be used across multiple industries, such as agriculture, biology, chemistry, engineering, and social sciences.

Double-blind studies are used primarily by the pharmaceutical industry because researchers can look directly at the impact of medications. 

Disadvantages

Inability to blind.

In some types of research, specifically therapeutic, the treatment cannot always be disguised from the participant or the experimenter. In these cases, you must rely on other methods to reduce bias.

Additionally, imposing blinding may be impossible or unethical for some studies. 

Double-blinding can be expensive because the researcher has to examine all the possible variables and may have to use different groups to gather enough data. 

Small Sample Size

Most double-blind studies are too small to provide a representative sample. To be effective, it is generally recommended that double-blind trials include around 100-300 participants.

Studies involving fewer than 30 participants generally can’t provide proof of a theory. 

Negative Reaction to Placebo

In some instances, participants can have adverse reactions to the placebo, even producing unwanted side effects as if they were taking a real medication. 

It doesn’t reflect real-life circumstances

When participants receive treatment or medication in a double-blind placebo study, each individual is told that the item in question might be real medication or a placebo.

This artificial situation does not represent real-life circumstances because when a patient receives a pill after going to the doctor in the real-world, they are told that the product is actual medicine intended to benefit them.

When situations don’t feel realistic to a participant, then the quality of the data can decrease exponentially.

What is the difference between a single-blind, double-blind, and triple-blind study?

In a single-blind study, the experimenters are aware of which participants are receiving the treatment while the participants are unaware.

In a double-blind study, neither the patients nor the researchers know which study group the patients are in. In a triple-blind study, neither the patients, clinicians, nor the people carrying out the statistical analysis know which treatment the subjects had.

Is a double-blind study the same as a randomized clinical trial?

Yes, a double-blind study is a form of a randomized clinical trial in which neither the participants nor the researcher know if a subject is receiving the experimental treatment, a standard treatment, or a placebo.

Are double-blind studies ethical?

Double blinding is ethical only if it serves a scientific purpose. In most circumstances, it is unethical to conduct a double-blind placebo controlled trial where standard therapy exists.

What is the purpose of randomization using double blinding?

Randomization with blinding avoids reporting bias, since no one knows who is being treated and who is not, and thus all treatment groups should be treated the same. This reduces the influence of confounding variables and improves the reliability of clinical trial results.

Why are double-blind experiments considered the gold standard?

Randomized double-blind placebo control studies are considered the “gold standard” of epidemiologic studies as they provide the strongest possible evidence of causality.

Additionally, because neither the participants nor the researchers know who has received what treatment, double-blind studies minimize the placebo effect and significantly reduce bias.

Can blinding be used in qualitative studies?

Yes, blinding is used in qualitative studies .

Cakir, S., Hepguler, S., Ozturk, C., Korkmaz, M., Isleten, B., & Atamaz, F. C. (2014). Efficacy of therapeutic ultrasound for the management of knee osteoarthritis: a randomized, controlled, and double-blind study. American journal of physical medicine & rehabilitation , 93 (5), 405-412.

Kobak, K. A., Taylor, L. V., Bystritsky, A., Kohlenberg, C. J., Greist, J. H., Tucker, P., … & Vapnik, T. (2005). St John’s wort versus placebo in obsessive–compulsive disorder: results from a double-blind study. International Clinical Psychopharmacology , 20 (6), 299-304.

Papachristofilou, A., Finazzi, T., Blum, A., Zehnder, T., Zellweger, N., Lustenberger, J., … & Siegemund, M. (2021). Low-dose radiation therapy for severe COVID-19 pneumonia: a randomized double-blind study. International Journal of Radiation Oncology* Biology* Physics , 110 (5), 1274-1282. Rostock, M., & Huber, R. (2004). Randomized and double-blind studies–demands and reality as demonstrated by two examples of mistletoe research. Complementary Medicine Research , 11 (Suppl. 1), 18-22.

Placebos, Drug Effects, and Study Design: A Clinician’s Guide

Information & authors, metrics & citations, view options, why are placebos necessary, predicting patients who will benefit from placebo, identifying placebo effects in patients, can we identify patients for whom immediate medication prescription may not be necessary, contrasting medication and psychotherapy: the role of placebos, are active placebos necessary, is placebo use ethical when effective treatments exist, summary and conclusions.

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18 How to run a placebo study: A closer look into complex experimental designs

• Published: December 2020
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This chapter is addressed to those who want to run a study aimed at identifying the underlying mechanisms of placebo effects. To study a placebo effect requires specific designs that cannot be performed in the classic clinical trial setting. Complex experimental designs are particularly necessary when one wants to investigate the neurobiological mechanisms, for example by means of agonist and antagonist drugs. Complex pharmacological designs have used up to twelve experimental arms (groups) in order to answer specific questions. To study the role of learning in placebo effects, for example conditioning, one needs to control the associations between conditioned and unconditioned stimuli both in the experimental and in the clinical setting. In addition, several approaches are possible for hiding a therapy from the subject’s view, so that he is totally unaware that a treatment is being performed, thus allowing the investigation of placebo effects without the administration of placebos.

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The difference between ‘placebo group’ and ‘placebo control’: a case study in psychedelic microdosing

Balázs szigeti.

1 Centre for Psychedelic Research, Imperial College London, London, UK

Robin Carhart-Harris

2 Psychedelics Division, Neuroscape, Department of Neurology, University of California San Francisco, San Francisco, USA

David Erritzoe

Associated data.

The data and software used here is available for scientific and research purposes at https://github.com/szb37/CorrectGuessRateCurve . The repository contains a conda computational environment, the data analyzed and scripts to reproduce all figures and major statistical findings described here.

In medical trials, ‘blinding’ ensures the equal distribution of expectancy effects between treatment arms in theory; however, blinding often fails in practice. We use computational modelling to show how weak blinding, combined with positive treatment expectancy, can lead to an uneven distribution of expectancy effects. We call this ‘activated expectancy bias’ (AEB) and show that AEB can inflate estimates of treatment effects and create false positive findings. To counteract AEB, we introduce the Correct Guess Rate Curve (CGRC) , a statistical tool that can estimate the outcome of a perfectly blinded trial based on data from an imperfectly blinded trial. To demonstrate the impact of AEB and the utility of the CGRC on empirical data, we re-analyzed the ‘self-blinding psychedelic microdose trial’ dataset. Results suggest that observed placebo-microdose differences are susceptible to AEB and are at risk of being false positive findings, hence, we argue that microdosing can be understood as active placebo. These results highlight the important difference between ‘ trials with a placebo-control group ’, i.e., when a placebo control group is formally present, and ‘ placebo-controlled trials ’, where patients are genuinely blind. We also present a new blinding integrity assessment tool that is compatible with CGRC and recommend its adoption.

Introduction

In medical research the gold standard experimental design is the blinded randomized controlled trial 1 , where ‘blinding’ refers to the concealment of the intervention 2 . The purpose of blinding is to equally distribute expectancy effects between treatment arms 3 , thus, to eliminate biases associated with expectancy. ‘Blinding integrity’ refers to how successfully blinding is maintained. Blinding integrity can be assessed by asking blinded parties, e.g., patients and/or doctors, to guess treatment allocation. If the correct guess rate (CGR) is higher than chance, then, blinding is ineffective. Assessing blinding integrity could be especially important when outcomes are subjective, for example in pain and psychiatric research, where there is a high susceptibility to expectation biases 4 . In these domains, only 2–7% of trials report blinding integrity and when blinding is assessed, it is found to be ineffective for about 50% of the trials 5 – 9 .

Poor reporting of blinding integrity may be explained by at least three factors. First, there is no accepted standard for how to assess blinding integrity. Most commonly, patients are asked to guess their treatment after the trial has concluded, but such data may be subject to recall and other biases 10 – 12 . Secondly, there is no accepted standard for how to incorporate blinding integrity into data analysis. Even if blinding integrity is assessed, most scientific reports do not attempt to incorporate blinding integrity data into the interpretation of the results. Finally, others have speculated that a reluctance to assess blinding stems from a fear that weak blinding could cast doubt on positive trial outcomes 5 . Supporting this reasoning, lesser blinding integrity reporting has been associated with industry sponsorship 6 , 9 .

There is a resurgent interest in the medicinal potential of psychedelic drugs, such as LSD and psilocybin 13 . Recently, ‘microdosing’ has emerged as a new paradigm for psychedelic use. Microdosing does not have a universally accepted definition, but most microdosers take oral doses of 10–20 μg LSD or 0.1–0.3 g of dried psilocybin containing mushrooms, 1–4 times a week 14 . Anecdotal claims have been made that microdosing improves well-being and cognition 15 , 16 . Observational studies have generally confirmed the positive anecdotal claims 17 – 20 , but so far placebo-controlled studies have failed to find robust evidence for larger than placebo efficacy in healthy samples 21 – 25 .

We recently conducted a ‘self-blinding citizen science trial’ on microdosing, where participants implemented their own placebo control based on online setup instructions without clinical supervision 24 . The strength of this design is twofold: it tested the effects of microdosing in a real-life context, increasing the trial’s external validity 26 , and it allowed us to obtain a large sample size while implementing placebo control at minimal logistic and economic costs. The study was completed by 191 participants, making it the largest placebo-controlled trial on psychedelic microdosing for a fraction of the cost of even a small traditional clinical trial.

Activated expectancy bias (AEB) model

We introduce a theoretically motivated computational model of AEB, the model’s structure and equations are shown on Fig.  1 , the key model features are:

• The presence or lack of side effects allow patients to infer their treatment at a higher than chance rate. The correct guess probability, p CG , in the model is 0.7, which is consistent with both microdosing 21 , 24 and antidepressants 27 – 29 trials.
• AEB model parameters are calibrated such that the treatment effect is 3 points, corresponding to a small-moderate effect size of 0.4 standardized mean difference, which is consistent with microdosing 21 , 22 , 24 and antidepressant trials 30 , numeric parameters can be found in Supplementary Table 1 .
• Patients have higher efficacy expectations for the active treatment than for placebo treatment, this positive expectancy bias is represented by the N AEB term in the model, see Fig.  1 .

The activated expectancy bias (AEB) model, consisting of 3 binary nodes (TRT, PT and TE) and a continuous value node, the outcome (OUT). In the equations, B X / N X stand for a random Bernoulli/normal variable, respectively. The binary nodes (TRT, PT and TE) represent Bernoulli variables (B TRT , B PT , B TE ), where the values of 0/1 correspond to placebo/active. To generate AEB model data, first Treatment (TRT) is determined by Eq. 1 and then the Perceived treatment (PT) by Eq. 2, where p CG is the probability of correct guess, i.e. the correct guess rate, and then Treatment expectancy is fixed according to Eq. 3. Finally, the outcome score is calculated by Eq. 4 which has components of natural history ( N NH ), direct treatment effect ( N DTE ) and activated expectancy bias ( N AEB ), see Supplementary table 1 for the numeric value of all parameters.

The AEB model was used to generate pseudo-experimental data with 2*2 = 4 parameter configurations, corresponding to direct treatment effect and activated expectancy bias being either active or not, see Fig.  1 . In our analysis the direct treatment effect (blue)/activated expectancy bias (red) pathways are turned off by setting the mean N DTE / N AEB equal to 0. For each configuration, 500 trials were simulated, each with 230 patients, mimicking the sample size of the microdose trial analyzed.

Self-blinding microdose trial

The self-blinding microdose trial used an 'self-blinding' citizen science approach, where participants implemented their own placebo control based on online setup instructions without clinical supervision 24 . Self-blinding involved enclosing the microdoses inside non-transparent gel capsules and using empty capsules as placebos. Then, these capsules were labeled with QR codes that allowed investigators to track when placebo/microdose was taken without sharing this information with participants. Participants were followed throughout a 4-week dosing period, taking 2 microdoses/week in the active group. For each capsule taken, participants made a binary guess whether their capsule was placebo or microdose, see Supplementary materials for details.

Here, the trial’s acute and post-acute outcomes are re-analyzed. Acute measures were completed 2–6 h after ingestion of the capsule, while post-acute measures were taken the day after a capsule was taken. Acute outcomes were: positive and negative affect schedule (PANAS) 31 , cognitive performance score (CPS) and visual analogue scale items for mood , energy , creativity , focus , and temper . The CPS is an aggregated quantification of cognitive performance based on 6 computerized tasks ( spatial span, odd one out, mental rotations, spatial planning, feature match, paired associates ). Post-acute outcomes were: Warwick–Edinburgh mental well-being scale (WEMWB) 32 , quick inventory of depressive symptomatology (QIDS) 33 , state-trait anxiety inventory (STAIT) 34 and social connectedness scale (SCS) 35 . To simplify the current analysis, we only used data from the first week of the experiment, thus, each datapoint is independent and not confounded by order effects. This approach reduced the overall sample, but yielded almost identical qualitative conclusion as the full dataset. In the current analysis n = 233 datapoints were included.

The trial only engaged people who planned to microdose through their own initiative, but who consented to incorporate placebo control to their self-experimentation. The trial team did not endorse microdosing or psychedelic use and no financial compensation was offered to participants. The study was approved by Imperial College Research Ethics Committee and the Joint Research Compliance Office at Imperial College London (reference number 18IC4518). Informed consent was obtained from all subjects, the trial was carried out in accordance with relevant guidelines and regulations.

Estimate of treatment effects

Throughout this work treatment effects are estimated by an outcome  ~  treatment linear model, where outcome is a numeric, treatment is a binary variable (placebo or active treatment). In this manuscript ‘non-CGR adjusted analysis’ means that this model is fitted to empirical data, while ‘CGR adjusted analysis’ means that this model is fitted to the CGR adjusted pseudo-experimental data, see Correct guess rate curve section for details. Therefore, the CGR-adjusted treatment estimate/p-value is to the estimate/p-value associated with the treatment term in the model above, applied to data adjusted by the CGRC method. All linear models were implemented using the lme package (version 3.1–155) in R (v4.0.2).

Correct guess rate curve

We developed CGR adjustment, a novel statistical technique that can estimate the outcome of a perfectly blinded trial, based on data from an imperfectly blinded trial. Briefly, first the scores are separated into four strata corresponding to all four possible combinations of treatment and guess . Next, statistical models of these four strata are built using kernel density estimation (KDE). KDE estimates were implemented by the scikit-learn package (v1.0.2) in python (v3.7), all parameters were left at default value. Then, random samples are drawn from each strata, such that the combined sample has CGR = 0.5, mimicking a perfectly blinded trial, see Fig.  2 for a detailed explanation. Treatment estimates for other CGR values can be obtained in a similar manner by changing the number of samples drawn from each KDE. For example, a trial with CGR = 0.6 can be approximated by drawing 0.6* n random samples from the correct guess KDEs and 0.4* n random samples from the incorrect guess KDEs, etc.

Correct guess rate (CGR) adjustment to estimate the outcome of a perfectly blinded trial based on data from an imperfectly blinded trial. First, scores (purple histogram at top) are separated into four strata corresponding to all possible combinations of treatment and guess . Both treatment and guess are binary with potential values of placebo/active, thus, the four strata are (using the treatment / guess notation): PL/PL, AC/PL, PL/AC and AC/AC. Next, statistical models of these strata are built using kernel density estimation (KDE). Note that two strata correspond to correct guesses (PL/PL and AC/AC; red) and two to incorrect guesses (AC/PL, PL/AC; blue). Next, n/2 random samples are drawn from the correct guess KDEs, such that the relative sample sizes of the correct guess strata are preserved, i.e. the ratio n PL/PL /n AC/AC is same as in the original data, see Supplementary materials for a numeric example. Similarly, n/2 random samples are drawn from the incorrect guess KDEs, such that the ratio n AC/PL /n PL/AC is same as in the original data. These random samples are then combined, resulting in a pseudo-experimental dataset with CGR = 0.5 (purple distribution at bottom), corresponding to effective blinding. The random sampling from KDEs is repeated 100 times, for each CGR-adjusted pseudo-experimental dataset is analyzed to estimate the direct treatment effect, see Estimate of treatment effects . The ‘CGR adjusted treatment effect/p-value’ is the mean treatment estimate / p-value across these 100 samples. Estimates at other CGR values can be obtained similarly, e.g. a trial with CGR = 0.6 can be approximated by drawing 0.6* n random samples from the correct guess KDEs and 0.4* n random samples from the incorrect guess KDEs, etc.

Correct guess rate (CGR) adjustment of the activated expectancy bias (AEB) model

We analyze pseudo-experimental data generated by the 2*2 = 4 configurations of the AEB model (corresponding to direct treatment effect and activated expectancy bias either being active or not, see Fig.  1 ) with both traditional, i.e. non-CGR adjusted, and CGR-adjusted analysis. To demonstrate that the qualitative conclusions presented here do not require fine tuning of parameters, we present a robustness analysis in the Supplementary Materials.

First, the case was analyzed where neither direct treatment effect nor the activated expectancy bias pathways are activated (top row in Table ​ Table1). 1 ). In this case, the outcome is a normal random variable. The treatment p-value was significant for 5%/6% of the simulated trials using the traditional/CGR adjusted models, which is expected based on the 0.05 significance level.

Correct guess rate (CGR) curves of the activated expectancy bias (AEB) model. Each panel shows the estimated treatment p-value (blue; scale shown on left y-axis) and effect size (red; scale shown on right y-axis), with their corresponding confidence interval, as a function of CGR. Horizontal purple dashed line represents the p = .05 significance threshold, vertical green dashed line corresponds to the simulated trial’s original CGR, while the black dashed line corresponds to a perfectly blinded trial (CGR = 0.5). The model was analyzed with 2*2 = 4 configurations of parameters, corresponding to the possibilities of the direct treatment effect (DTE) and activated expectancy bias (AEB) either being active or inactive, see Fig.  1 . For the DTE off; AEB on case (bottom left) generates a false positive finding when CGR is not considered during analysis (green dashed line intersects p-value estimate below 0.05), but CGR adjustment recovers the lack of treatment effect (black dashed line intersects p-value estimate above 0.05). For the DTE on; AEB on case (bottom right), both analyses correctly identify that there is a treatment effect; however, non-CGR adjusted analysis overestimates the effect size by ~ 40%, see Table ​ Table1 1 for numeric results.

Comparative results of traditional and CGR adjusted analysis of the AEB model.

The model is analyzed with 2*2 = 4 parameter configurations, corresponding to the direct treatment effec t (DTE) and activated expectancy bias being active or not, see Fig.  1 . Results are equivalent for the two analysis in the top two rows, however, when only the activated expectancy bias is active (3rd row from top), traditional analysis produces false positive findings for 78% of the simulations. Furthermore, when both direct treatment effect and activated expectancy bias are active (bottom row), traditional analysis overestimates the known true treatment effect (estimate is 5.69 points, while the true effect is 3 points), see Fig.  3 for the corresponding CGR curves.

Next, the case was analyzed where a direct treatment effect was active, but activated expectancy bias was not active (second row from top in Table ​ Table1). 1 ). Non-CGR adjusted and CGR adjusted analysis identifies a significant treatment effect in 86/84% of the simulations with an average p-value of 0.032/0.036, respectively. We note that this 14%/16% false negative rate is due to the small effect used in simulations (~0.4 Hedges’ g), larger effects decrease the false negative rate of both analyses, see robustness analysis in Supplementary materials. In both analysis the treatment estimate is within 5% of the true effect.

Next, the case was analyzed where a direct treatment effect was inactive, but activated expectancy bias was active (third row from top in Table ​ Table1), 1 ), i.e. a scenario where there is no true treatment effect and activated expectancy is a complete mediator of the treatment. For the traditional models, 78% of the simulated trials resulted in a false positive treatment effect. For the CGR-adjusted models, only 3% of the simulated trials produced a false positive treatment effect.

Finally, the case was analyzed where both a direct treatment effect and activated expectancy bias were active (bottom row in Table ​ Table1), 1 ), i.e., a case where AEB is a partial mediator of treatment. The average treatment p-value was 0.001/0.041 with 99%/82% of the trials resulting a significant treatment effect for the traditional/CGR adjusted analysis, respectively. Note that the CGR adjusted analysis can only be as good to detect a treatment effect as the unadjusted analysis when only DTE is active (as the adjustment aims to remove the effect of AEB). Thus, CGR adjusted analysis detects an effect in just 4% less of the simulations (86% vs. 82%) than this best-case scenario, i.e. CGR adjustment only adds 4% to the false negative rate. Furthermore, the traditional analysis estimated the effect to be 5.69 points, while the CGR adjusted estimate was 3.04 points (the true treatment effect was 3), so traditional analysis significantly overestimated the effect due to the influence of AEB. In summary, the CGR adjusted analysis’ false negative rate is ~2-4% higher than the traditional analysis’ (rows 2&4 in Table ​ Table2), 2 ), but the false positive rate is ~75% lower when AEB is present (row1&3 in Table ​ Table2). 2 ). Furthermore, when a true effect is present, CGR provides a more reliable estimate of the effect size (row 4 in Table ​ Table2) 2 ) as it subtracts the influence of AEB.

Comparison of traditional (non-CGR adjusted) and CGR adjusted models of the self-blinding microdose trial data.

Note that for all outcomes that were statistically significant in the traditional models became insignificant after CGR adjustment with the exception of the energy VAS. These results argue that positive outcomes in the traditional analysis could be false positive findings created by AEB. Energy VAS remained significant even after CGR adjustment, although the effect size is reduced by ~ 40%. This finding suggests that microdosing increases self-perceived energy beyond what is explainable by expectancy effects, although the remaining effect is small, see Fig.  4 for CGR curves of selected outcomes.

Correct guess rate (CGR) adjusted analysis of the self-blinding microdose trial

Next, we advance from analyzing pseudo-experimental data to scrutinizing empirical data from the self-blinding microdose trial 24 . Using traditional, i.e. non-CGR adjusted, data analysis, statistically significant placebo-microdose differences were observed on the following scales: acute emotional state (PANAS; mean difference ± SE = 3.2 ± 1.3; p = 0.01**), energy visual analogue scale VAS (11.5 ± 2.7; p < 0.001***), mood VAS (6.4 ± 2.7; p = 0.02*), creativity VAS (6.4 ± 2.5; p = 0.01*) and post-acute depression (QIDS; − 1.2 ± 0.06; p = 0.04*).

After CGR adjustment, none of these outcomes remained significant with the exception of the energy VAS that remained significant (p ~ 0.04), but with a ~ 40% reduced effect size.

This finding suggests that microdosing increases self-perceived energy beyond what is explainable by expectancy effects, although the magnitude of the remaining effect is small (Hedges’ g = 0.34). Equivalence testing for all outcomes where significance changed after CGR adjustment (i.e. PANAS , QIDS , mood and creativity VASs) with an equivalence bound equal to the average within-subject variability were significant, arguing that outcomes were equivalent in the placebo and microdose groups after the CGR adjustment, see Supplementary materials for details. See Table ​ Table2 2 for numeric results and Fig.  4 for the CGR curves of selected outcomes.

Correct guess rate (CGR) curves for self-blinding microdose trial outcomes. Each panel shows the estimated treatment p-value (blue; scale shown on left y-axis) and effect size (red; scale shown on right y-axis), with their corresponding confidence interval, as a function of CGR. Horizontal purple dashed line represents the p = .05 threshold, vertical green dashed line corresponds to the trial’s original CGR (= 0.72), while the black dashed line corresponds to a perfectly blinded trial (CGR = 0.5). Outcomes in the top row ( Positive and Negative Affection Scale (PANAS) and Mood visual analogue scale ) are significant according to unadjusted analysis (green dashed line intersects p-value estimate below 0.05), but become insignificant after CGR adjustment (black dashed line intersects p-value estimate above 0.05), arguing that these findings could be false positives driven by AEB. Energy VAS remains significant even after CGR adjustment, although the effect size is reduced by ~ 40%. This finding suggests that microdosing increases self-perceived energy beyond what is explainable by expectancy effects, although the remaining effect is small (Hedges’ g = .34). Finally, CGR adjustment has little impact on the cognitive performance score as both the p-value and the effect estimate remain close to a constant. This finding suggests that this measure is not affected by AEB, possibly because cognitive performance was not self-rated, rather measured by objective computerized tests, see Table ​ Table2 2 for numerical results.

Treatment guess questionnaire

In the supplementary materials we included a brief, 5-items questionnaire developed to collect treatment guess and source of unblinding data. The resulting data is compatible with the current and planned future versions of the CGR curve.

Effective blinding distributes expectancy effects equally between treatment arms 3 . However, if blinding is ineffective, i.e. patients can deduce their treatment allocation, and if patients have a positive expectancy bias for the active arm, then expectancy effects will be no longer equally distributed and trial outcomes will be biased towards the active arm. We call this bias ‘activated expectancy bias’ (AEB), which can be viewed as a residual expectancy bias potentially present even in ‘blinded’ trials. A key consequence is that the research community needs to distinguish between trials with a placebo-control group, i.e., when a placebo control group is formally present in the trial , and placebo-controlled trials , where patients are genuinely blinded and thus AEB is not present. In other words, a placebo control group is necessary, but in-itself insufficient to control for expectancy effects. For example, a recent trial on LSD therapy includes ‘double-blind, placebo-controlled’ in its title, but as the manuscript describes "only one patient in the LSD-first group mistook LSD as placebo” (out of 18 patients), highlighting that the trial was formally blinded, but not in practice 36 . The implication is that ‘placebo-controlled’ studies are more fallible than conventionally assumed with consequences for evidence-based medicine.

Current FDA drug approval only requires two trials with statistically significant drug-placebo difference 37 , thus, the self-blinding microdose trial yielded evidence consistent with FDA approval, despite that the findings were likely false positives, driven by AEB. In our view, placebo-controlled trials should only be considered ‘gold standard’ if blinding integrity is demonstrated with empirical data. This requirement would create a new, more rigorous standard for what is ‘placebo control’. Given the high costs and low success rate of psychiatric trials 38 , there may be little appetite from industry and regulators to create such new standard, but it should be embraced by the scientific community.

We note that it is difficult to estimate how prevalent AEB is in medical trials, because blinding integrity has only been reported in 2–7% of trials 5 , 6 , 9 . To understand the prevalence of AEB, more trials need to capture blinding integrity data 39 . To aid this practice, in the supplementary materials we suggest a brief 5-items questionnaire that is compatible with the method presented here and recommend its adoption.

When the self-blinding microdose trial was analyzed traditionally, small, but significant microdose-placebo differences were observed on emotional state, depression, mood, energy and creativity, favoring microdosing 24 . After CGR adjustment, only energy VAS remained significant (p ~ 0.04) with a ~ 40% reduced effect size—we note that another recent trial similarly found significant increases in self-perceived energy beyond what is explainable by the placebo and expectancy effects 40 . One could argue that these negative results are false negatives; however, the consistency of the negative results across measures argues against this possibility. Furthermore, the trial had the necessary features for AEB, i.e. weak blinding and a positively biased 24 , implying that the trial is susceptible to AEB. AEB is likely to be present in other psychedelic microdose trials as well, results should be interpreted with caution, especially if evidence for effective blinding is not presented.

We hypothesize that the reported benefits psychedelic microdosing on mood and creativity can be understood as an ‘active placebo’, i.e., an intervention without medical benefits , but with perceivable effects 36 , 39 , 40 , emphasizing the difference between effects and benefits . A recent comprehensive review of microdosing concluded that: “These findings together provide clear evidence of psychopharmacological effects. That is, microdosing is doing something. A key question for researchers is whether the effects of microdosing have clinical or optimization benefits beyond what might be explained by placebo or expectation.” 41 . In short, microdosing leads to perceivable effects , for example by the heightened energy levels, explaining why CGR is universally high across trials 21 , 24 , 40 , but at this point none of these effects seem to be related improved mental health. If our hypothesis is correct, then, either improved blinding or a sample without positive expectancy would nullify the observed benefits of microdosing by nullifying AEB. An alternative possibility is that microdosing is only effective at doses where blinding integrity cannot be maintained due to conspicuous subjective effects, such as in the case of psychedelic macrodosing 42 . In this scenario the possibility of effective placebo control is abandoned and efficacy beyond expectancy needs to be established outside of blinded trials. Arguments for the merit of alternative trial designs to assess the efficacy of psychedelics have been made before 43 , for example mechanistic studies could also help to establish the causal effect of treatment. Recently, arguments against the value of placebo control have been raised in psychedelic trials 44 . This article remains neutral on this issue, it merely insists that if a trial is called ‘placebo controlled', then it should really control for the placebo effect and not just have a ‘placebo group'.

Our arguments above assume that the high CGR is explained by malicious unblinding , i.e. positive treatment expectancy drives the positive outcomes, rather than benign unblinding , i.e. patients correctly guess their treatment due to noticeable health improvements 45 . If unblinding is benign, then CGR adjustment could lead to false negative findings due to collider bias 46 (currently Fig.  1 represents malicious unblinding , for benign unblinding PT → TE → OUT would need to be replaced with OUT → PT). Accordingly, investigators need to carefully assess the source of unblinding prior to using our method. To facilitate this assessment, our questionnaire in the supplementary materials captures this source of unblinding information.

What was the source of unblinding in the self-blinding psychedelic microdose trial? Two lines of evidence point towards that it was the perceptual/side effects rather than efficacy, corresponding to malicious unblinding. First, 55% reported that the primary cue to formulate their treatment guess was ‘ body/perceptual sensations’ , such as muscle tension (58%) and stomach discomfort (27%), in contrast only 23% reported ‘ mental/psychological benefits’ . Secondly, among participants who were assessed under both placebo and microdose conditions, the mean placebo-microdose difference on the positive / negative affect subdomains of the PANAS was 2.1/0.8. In a recent study without any intervention, the mean temporal intra-individual difference, i.e. the within-subject day-to-day variability, of the same subdomains was ~ 10/~ 6 47 . Thus, the natural within-subject variability is ~ 500–750% larger than the mean placebo-microdose difference, arguing that the effect is too small to be noticeable.

Limitations

CGR adjustment relies on binary treatment guess data from patients, however, treatment belief is a complex construct that cannot be reduced to a single binary variable. We focused on binary guess data due to its availability and note that even this imperfect data is rare to find. Treatment guess could be better characterized if guess confidence was also rated. Such confidence data would allow to distinguish between those who truly identified their drug condition (high confidence guess) versus those who guess correctly by chance (low confidence guess).

In our analysis, we treat the source of unblinding as a binary variable, either being only benign or malicious. A more realistic scenario is that for some patients, both efficacy and non-specific effects contribute to their guesses. Relatedly, our assessment on the source of unblinding is based on retrospective self-reports, that cannot provide conclusive evidence on causation.

Our AEB model assumes linear addition of the direct treatment and the activated expectancy effects to estimate the total effect, however, these effects may not be additive for all circumstances 48 .

The CGR curve relies on resampling the observed data, thus, the resulting data cannot be considered experimentally randomized, and as a consequence confounding variables may not be equally distributed. Despite the KDE approximation of each strata, practically some datapoints may appear multiple times in the pseudo-experimental samples, potentially increasing the error rate due to dependent observations. The error rate of our methodology is a function of the sample characteristics, generally, the smaller the sample, the more extreme the CGR and the smaller the effects are, the less reliable the results will be. In a range of these parameters that mimics microdosing and antidepressant trials (n ~ 200, CGR ~ 0.7, treatment effect ~ 0.4 Hedges’ g), our method has comparable false negative rate as traditional, non-CGR adjusted analysis. However, when AEB is present CGR adjusted analysis has a much lower false positive rate and a more reliable estimate of the true effect size compared to non-CGR adjusted analysis. The error rate of our methodology can be higher in other contexts, in particular if the sample is small. Researchers wishing to use CGR adjustment should first run simulations to determine whether CGR produces acceptable error rates for the parameters of their data and the application in mind. For the limitations listed above, our CGR adjustment is inferior to results from a truly blind RCT, its value lies that it can provide an approximate answer when achieving ideal blinding is difficult or impossible.

CGR adjustment can be viewed as an example of a resampling method to overcome the challenges of imbalanced data. Here we present only a particular solution to this problem and not a systematic exploration of how rebalancing of the data can be achieved.

Finally, our data on microdosing was obtained from a self-selected healthy sample. Microdosing may be effective for certain conditions in a clinical population, in domains we did not assess, if used at higher doses or longer time periods or when it is co-administered with a behavioral therapy, such as cognitive training.

Supplementary Information

Acknowledgements.

We would like to acknowledge Allan Blemings, Fernando Rosas and Laura Kartner for the stimulating discussions that inspired this work.

Author contributions

B.S. did the conceptualization, investigation, formal analysis, software, visualization, wrote original draft and reviewed/edited the manuscript. D.N., R.C.H. and D.E. supervised the work and reviewed/edited the manuscript.

Data availability

Competing interests.

B.S. declares no conflict. D.N. is an advisory to COMPASS Pathways, Neural Therapeutics, and Algernon Pharmaceuticals; received consulting fees from Algernon, H. Lundbeck and Beckley Psytech; received lecture fees from Takeda and Otsuka and Janssen plus owns stock in Alcarelle, Awakn and Psyched Wellness. D.E. received consulting fees from Aya, Mindstate, Field Trip, Clerkenwell Health. R.C.H. is an advisor to Beckley Psytech, Mindstate, TRYP Therapeutics, Mydecine, Usona Institute, Synthesis Institute, Osmind, Maya Health, and Journey Collab.

Publisher's note

Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.

The online version contains supplementary material available at 10.1038/s41598-023-34938-7.

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Experimental vs. control group explained.

Home » Experimental vs. Control Group Explained

Group Comparison Analysis plays a pivotal role in experimental research. By examining the differences between experimental and control groups, researchers can draw meaningful conclusions about specific interventions. This process helps in determining whether observed effects are indeed attributable to the treatment or merely due to chance.

In any experiment, understanding how participants respond to different conditions is crucial. Group Comparison Analysis allows scientists to tease apart these responses, yielding insights that can inform various fields. Ultimately, this analytical approach not only enhances the validity of research findings but also supports the development of effective strategies based on empirical evidence.

The Basics of Experimental Groups

In research, understanding the distinction between experimental groups is essential for accurate findings. An experimental group consists of participants exposed to a variable being tested, while a control group serves as the baseline for comparison. This design enhances the reliability of results by isolating the effects of the independent variable. To conduct a thorough group comparison analysis, researchers need to ensure that both groups are similar in characteristics, minimizing biases.

The selection of participants plays a crucial role in the integrity of the study. Random assignment helps to ensure that individuals in both groups do not display pre-existing differences. This allows researchers to draw valid conclusions regarding the impact of the experimental treatment. Analyzing data from both groups provides insights into whether the intervention produces the expected changes. Effective comparison between these groups is foundational for advancing scientific knowledge. Understanding these basics will guide you through interpreting research outcomes with confidence.

Definition and Purpose

Understanding the experimental and control groups is essential in any Group Comparison Analysis. The experimental group receives the treatment or intervention, while the control group serves as a baseline for comparison. This structure is pivotal in determining the effectiveness of a given treatment and minimizes bias, ensuring the results are reliable.

The purpose of utilizing these groups lies in establishing a clear cause-and-effect relationship. By comparing outcomes from both groups, researchers can identify any significant differences attributable to the treatment. This comparison not only enhances the validity of findings but also influences data-driven decisions in various fields, including healthcare and marketing. Ultimately, the insight gained from this method fosters informed strategies that can lead to improved outcomes, whether in product development or user experience.

Designing an Experimental Group: Group Comparison Analysis

Designing an experimental group involves carefully planning each aspect to ensure valid results through group comparison analysis. This analysis is crucial for distinguishing the effects of a treatment or intervention from the natural variability found in any population. To effectively design your experimental group, you need to determine the characteristics that will make it comparable to the control group.

A proper comparison requires selection criteria such as age, gender, and baseline characteristics. This helps ensure that differences in outcomes arise solely from the intervention rather than from pre-existing variances. Next, consider randomization; randomly assigning participants reduces bias and enhances the study's reliability. Lastly, maintaining consistency in treatment delivery is essential. This ensures that everyone in the experimental group receives the same intervention, thus allowing for an accurate analysis of effects. By following these principles, your group comparison analysis can yield insightful and actionable outcomes.

The Role of Control Groups in Research

Control groups play a vital role in research by providing a benchmark to which experimental groups can be compared. Through group comparison analysis, researchers can discern the effects of an intervention by measuring outcomes against the control group that does not receive the treatment. This approach ensures that any observed changes in the experimental group can be more confidently attributed to the treatment rather than other external factors.

Moreover, control groups help minimize bias and variability in research outcomes. By allowing researchers to assess how participants behave under standard conditions, it becomes easier to isolate the impact of the experimental variable. Understanding these dynamics improves the reliability of results, making findings more valid and generalizable. Therefore, incorporating control groups in studies is essential for achieving accurate and trustworthy conclusions that can inform future practices or theories.

Definition and Purpose of Control Groups in Group Comparison Analysis

Control groups are essential in group comparison analysis, serving as benchmarks for experimental outcomes. These groups consist of participants who do not receive the treatment or intervention under investigation, allowing researchers to isolate the impact of specific variables. By comparing the results from the experimental group against the control group, researchers can determine the effectiveness of the intervention in a more precise manner.

The purpose of control groups is to minimize biases and ensure valid conclusions. They help in identifying whether observed changes in the experimental group are genuinely caused by the treatment or merely due to external factors. Additionally, control groups enable replication of studies, which is vital for affirming findings and fostering scientific credibility. In summary, control groups are indispensable tools in group comparison analysis, providing clarity and enhancing the reliability of research outcomes.

Examples of Control Group Usage

Control groups are essential in various fields, enabling researchers to validate their findings by providing a baseline for comparison. For instance, in a clinical trial assessing a new medication, one group receives the drug while a control group receives a placebo. This setup allows for a clearer understanding of the drug's effectiveness versus no treatment at all.

In market research, control groups allow analysts to examine consumer behavior under different conditions. A common example is testing two marketing strategies: one group receives traditional ads, while the control group is exposed to digital campaigns. Group comparison analysis reveals which method resonates better with the audience, helping to refine marketing approaches and optimize future campaigns. Through these examples, it's evident that control groups are invaluable in ensuring scientific rigor and making informed decisions across various domains.

Conclusion: The Importance of Group Comparison Analysis in Research

Group Comparison Analysis serves as a critical tool for researchers, allowing them to discern the differences between experimental and control groups. By methodically comparing these groups, researchers can assess the effectiveness of interventions or treatments. This type of analysis provides vital insights, facilitating a deeper understanding of how variables impact outcomes.

Furthermore, the importance of this analysis extends beyond mere statistical significance. It fosters evidence-based decision-making, ensuring that findings are reliable and applicable in real-world settings. Ultimately, understanding the dynamics between different groups equips researchers with the knowledge to make informed conclusions, driving advancements in various fields of study.

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A randomized double-blind placebo-controlled clinical trial of Guanfacine Extended Release for aggression and self-injurious behavior associated with Prader-Willi Syndrome

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Introduction: Prader-Willi Syndrome (PWS), a rare genetic disorder, affects development and behavior, frequently resulting in self-injury, aggression, hyperphagia, oppositional behavior, impulsivity and over-activity causing significant morbidity. Currently, limited therapeutic options are available to manage these neuropsychiatric manifestations. The aim of this clinical trial was to assess the efficacy of guanfacine-extended release (GXR) in reducing aggression and self-injury in individuals with PWS. Trial Design: Randomized, double-blind, placebo-controlled trial conducted under IRB approval. Methods: Subjects with a diagnosis of PWS, 6-35 years of age, with moderate to severe aggressive and/or self-injurious behavior as determined by the Clinical Global Impression (CGI)-Severity scale, were included in an 8-week double-blind, placebo-controlled, fixed-flexible dose clinical trial of GXR, that was followed by an 8-week open-label extension phase. Validated behavioral instruments and physician assessments measured the efficacy of GXR treatment, its safety and tolerability. Results: GXR was effective in reducing aggression/agitation and hyperactivity/noncompliance as measured by the Aberrant Behavior Checklist (ABC) scales (p=0.03). Overall aberrant behavior scores significantly reduced in the GXR arm. Aggression as measured by the Modified Overt Aggression Scale (MOAS) also showed a significant reduction. Skin-picking lesions as measured by the Self Injury Trauma (SIT) scale decreased in response to GXR. No serious adverse events were experienced by any of the study participants. Fatigue /sedation was the only adverse event significantly associated with GXR. The GXR group demonstrated significant overall clinical improvement as measured by the CGI-Improvement (CGI-I) scale. (p<0.01). Conclusion: Findings of this pragmatic trial strongly support the use of GXR for treatment of aggression, skin picking, and hyperactivity in children, adolescents, and adults with PWS. Trial Registration: ClinicalTrials.gov Identifier - NCT05657860

Competing Interest Statement

I have read the journal's policy and the authors of this manuscript have the following competing interests: DS has served as a consultant to Soleno Therapeutics, Acadia Pharmaceuticals, Tonix Pharmaceuticals, and Consynance Therapeutics. MS and TJ have no other competing interests to report.

Clinical Trial

ClinicalTrials.gov identifier: NCT05657860

Funding Statement

Author declarations.

I confirm all relevant ethical guidelines have been followed, and any necessary IRB and/or ethics committee approvals have been obtained.

The details of the IRB/oversight body that provided approval or exemption for the research described are given below:

This study was approved by the Institutional Review Board of Maimonides Medical Center (# 2020-11-03-MMC). Written, IRB-approved informed consent was obtained from each participant's parent or legal guardian, and assent was obtained from each participant, as applicable.

I confirm that all necessary patient/participant consent has been obtained and the appropriate institutional forms have been archived, and that any patient/participant/sample identifiers included were not known to anyone (e.g., hospital staff, patients or participants themselves) outside the research group so cannot be used to identify individuals.

I understand that all clinical trials and any other prospective interventional studies must be registered with an ICMJE-approved registry, such as ClinicalTrials.gov. I confirm that any such study reported in the manuscript has been registered and the trial registration ID is provided (note: if posting a prospective study registered retrospectively, please provide a statement in the trial ID field explaining why the study was not registered in advance).

I have followed all appropriate research reporting guidelines, such as any relevant EQUATOR Network research reporting checklist(s) and other pertinent material, if applicable.

Data Availability

All relevant data are within the manuscript and its Supporting Information files and will be available upon its publication.

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Two Experimental HIV Vaccine Regimens Fail To Lower Infections In Three-Year Trial Compared To Participants Taking A Placebo In Eastern, Southern Africa, Study Shows

August 02, 2024

• Introduction
• Conclusions
• Article Information

The study had a run-in period (if stable conventional treatment was needed), a 4-week screening period, a 12-week double-blind treatment period, and a 3-week safety follow-up period (to day 105). The first patient signed the informed consent form on February 6, 2018, and the last patient completed the trial on December 16, 2020. During the double-blind treatment period, patients with active ulcerative colitis were randomized in a 1:1:1 ratio to receive olamkicept every 2 weeks at doses of 600 mg or 300 mg or placebo by intravenous infusion at days 0 (baseline), 14, 28, 42, 56, and 70. Disease activity was assessed at screening visit, baseline, and weeks 2 to 12. During screening and at week 12, assessments of disease activity included endoscopy (colonoscopy or sigmoidoscopy).

Clinical response at week 12 was defined as a decrease of 3 or greater and of 30% or greater from baseline in total Mayo score, including a decrease of 1 or greater from baseline in rectal bleeding subscore or of 1 or less1 in rectal bleeding subscore. Clinical remission at week 12 was defined as a total Mayo score of 2 or less, no individual subscore greater than 1, and a rectal bleeding subscore of 0. Mucosal healing at week 12 was defined as a Mayo endoscopic subscore of 0 or 1. Remission per modified Mayo score (ie, total Mayo score excluding Physician’s Global Assessment subscore) at week 12 was defined as a stool frequency subscore of 1 or less, a rectal bleeding subscore of 0, and an endoscopy subscore of 0 or 1. The 90% CI and P value for treatment difference were derived from a logistic regression model adjusted for treatment group, randomization stratification factors, and total Mayo score at baseline as covariates. The numbers of patients were based on the full analysis set, consisting of all randomized patients with at least 1 postbaseline 9-point partial Mayo score value, and patients with missing outcomes were imputed as nonresponders (4 patients in the olamkicept 600-mg group, 3 in the 300-mg group, and 8 patients in the placebo group).

The boxplots of Mayo scores per treatment group present the median (the horizontal line in the box), mean (the diamond in the box), and IQR (25th to 75th percentiles), with whisker length equal to 1.5 times the IQR and dots indicating outliers. Summaries were based on the full analysis set, and patients with missing outcomes were not imputed. Amount of missing at each visit in each treatment group can be quantified via the No. of patients.

eTable 1. Trial Protocol

Statistical Analysis Plan

eAppendix 1. List of Participating Institutions

eAppendix 2. Supplementary Methods

eAppendix 3. Pharmacokinetics, Pharmacodynamics, And Immunogenicity

eTable 1. Efficacy Outcomes in Full Analysis Set

eTable 2. Summary of Biomarker Changes from Baseline in Each Dose Group

eTable 3. Summary of Pharmacokinetic Parameters of Olamkicept in Serum (PKS)

eTable 4. Summary of Development of Anti-Drug Antibodies in Patients Receiving Olamkicept

eFigure 1. Study Schema

eFigure 2. Efficacy of Olamkicept 600 mg and Placebo by Subgroups

eFigure 3. Change from Baseline in Biomarkers Over Time

eFigure 4. Lipid Profiles, Platelet and Neutrophil Count Over Time

eFigure 5. Olamkicept Plasma Concentrations Over Time

Data Sharing Statement

• Effect of Fecal Microbiota Transplantation on 8-Week Remission in Patients With Ulcerative Colitis JAMA Preliminary Communication January 15, 2019 This randomized clinical trial compares the ability of anaerobically prepared pooled donor vs autologous fecal microbiota transplantation to induce remission in patients with ulcerative colitis (UC). Samuel P. Costello, MBBS; Patrick A. Hughes, PhD; Oliver Waters, MBBS; Robert V. Bryant, MScR; Andrew D. Vincent, PhD; Paul Blatchford, PhD; Rosa Katsikeros, BSc; Jesica Makanyanga, MBChB; Melissa A. Campaniello, BSc; Chris Mavrangelos, BSc; Carly P. Rosewarne, PhD; Chelsea Bickley, BSc; Cian Peters, MS; Mark N. Schoeman, PhD; Michael A. Conlon, PhD; Ian C. Roberts-Thomson, PhD; Jane M. Andrews, PhD
• Ulcerative Colitis in Adults JAMA JAMA Clinical Guidelines Synopsis September 22, 2020 This JAMA Clinical Guidelines Synopsis summarizes the American College of Gastroenterology’s 2019 guideline on ulcerative colitis in adults. Laura R. Glick, MD; Adam S. Cifu, MD; Lauren Feld, MD
• Ulcerative Colitis in Adults—A Review JAMA Review September 12, 2023 This review discusses the epidemiology, pathophysiology, diagnosis, and treatment of ulcerative colitis in adults. Beatriz Gros, MD; Gilaad G. Kaplan, MD, MPH
• Patient Information: Ulcerative Colitis JAMA JAMA Patient Page February 27, 2024 This JAMA Patient Page describes the condition of ulcerative colitis and its symptoms, diagnosis, and treatment options. Rebecca Voelker, MSJ

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Zhang S , Chen B , Wang B, et al. Effect of Induction Therapy With Olamkicept vs Placebo on Clinical Response in Patients With Active Ulcerative Colitis : A Randomized Clinical Trial . JAMA. 2023;329(9):725–734. doi:10.1001/jama.2023.1084

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Effect of Induction Therapy With Olamkicept vs Placebo on Clinical Response in Patients With Active Ulcerative Colitis : A Randomized Clinical Trial

• 1 Department of Gastroenterology, The First Affiliated Hospital, Sun Yat-sen University, Guangzhou, China
• 2 Department of Gastroenterology and Hepatology, General Hospital, Tianjin Medical University, Tianjin, China
• 3 Department of Gastroenterology, Affiliated ZhongDa Hospital, School of Medicine Southeast University, Nanjing, China
• 4 Department of Gastroenterology, Shengjing Hospital of China Medical University, Shenyang, China
• 5 Department of Gastroenterology, Sir Run Run Shaw Hospital, Zhejiang University, Hangzhou, China
• 6 Department of Gastroenterology, Ruijin Hospital, Shanghai Jiaotong University School of Medicine, Shanghai, China
• 7 Department of Oncology, National Taiwan University Hospital & College of Medicine, Taipei, China
• 8 Division of Gastroenterology and Hepatology, Renji Hospital, Shanghai Jiaotong University School of Medicine, Shanghai, China
• 9 Department of Gastroenterology, Bethune First Affiliated Hospital of Jilin University, Changchun, China
• 10 I-Mab Biopharma (Shanghai), Shanghai, China
• 11 I-Mab Biopharma (Hangzhou), Hangzhou, China
• 12 Department of Medicine I, University Hospital Schleswig Holstein, Kiel University, Kiel, Germany
• Preliminary Communication Effect of Fecal Microbiota Transplantation on 8-Week Remission in Patients With Ulcerative Colitis Samuel P. Costello, MBBS; Patrick A. Hughes, PhD; Oliver Waters, MBBS; Robert V. Bryant, MScR; Andrew D. Vincent, PhD; Paul Blatchford, PhD; Rosa Katsikeros, BSc; Jesica Makanyanga, MBChB; Melissa A. Campaniello, BSc; Chris Mavrangelos, BSc; Carly P. Rosewarne, PhD; Chelsea Bickley, BSc; Cian Peters, MS; Mark N. Schoeman, PhD; Michael A. Conlon, PhD; Ian C. Roberts-Thomson, PhD; Jane M. Andrews, PhD JAMA
• JAMA Clinical Guidelines Synopsis Ulcerative Colitis in Adults Laura R. Glick, MD; Adam S. Cifu, MD; Lauren Feld, MD JAMA
• Review Ulcerative Colitis in Adults—A Review Beatriz Gros, MD; Gilaad G. Kaplan, MD, MPH JAMA
• JAMA Patient Page Patient Information: Ulcerative Colitis Rebecca Voelker, MSJ JAMA

Question   Does olamkicept, a selective inhibitor of the soluble interleukin 6 (sIL-6R)/IL-6 complex, increase the likelihood of clinical response in patients with active ulcerative colitis?

Findings   In this randomized clinical trial that included 91 patients with active ulcerative colitis and an inadequate response to conventional therapy, biweekly intravenous infusion with olamkicept 600 mg, olamkicept 300 mg, and placebo resulted in clinical response rates of 58.6%, 43.3%, and 34.5%, respectively, at 12 weeks. Only the difference between 600 mg and placebo was statistically significant.

Meaning   Intravenous olamkicept 600 mg biweekly, compared with placebo, increased the likelihood of clinical response at 12 weeks in patients with active ulcerative colitis, but further research is needed for replication and to assess longer-term efficacy and safety.

Importance   Olamkicept, a soluble gp130-Fc-fusion-protein, selectively inhibits interleukin 6 (IL-6) trans-signaling by binding the soluble IL-6 receptor/IL-6 complex. It has anti-inflammatory activities in inflammatory murine models without immune suppression.

Objective   To assess the effect of olamkicept as induction therapy in patients with active ulcerative colitis.

Design, Setting, and Participants   Randomized, double-blind, placebo-controlled phase 2 trial of olamkicept in 91 adults with active ulcerative colitis (full Mayo score ≥5, rectal bleeding score ≥1, endoscopy score ≥2) and an inadequate response to conventional therapy. The study was conducted at 22 clinical study sites in East Asia. Patients were recruited beginning in February 2018. Final follow-up occurred in December 2020.

Interventions   Eligible patients were randomized 1:1:1 to receive a biweekly intravenous infusion of olamkicept 600 mg (n = 30) or 300 mg (n = 31) or placebo (n = 30) for 12 weeks.

Main Outcomes and Measures   The primary end point was clinical response at week 12 (defined as ≥3 and ≥30% decrease from baseline total Mayo score; range, 0-12 [worst] with ≥1 decrease and ≤1 in rectal bleeding [range, 0-3 {worst}]). There were 25 secondary efficacy outcomes, including clinical remission and mucosal healing at week 12.

Results   Ninety-one patients (mean age, 41 years; 25 women [27.5%]) were randomized; 79 (86.8%) completed the trial. At week 12, more patients receiving olamkicept 600 mg (17/29 [58.6%]) or 300 mg (13/30 [43.3%]) achieved clinical response than placebo (10/29 [34.5%]), with adjusted difference vs placebo of 26.6% (90% CI, 6.2% to 47.1%; P  = .03) for 600 mg and 8.3% (90% CI, −12.6% to 29.1%; P  = .52) for 300 mg. Among patients randomized to receive 600 mg olamkicept, 16 of 25 secondary outcomes were statistically significant compared with placebo. Among patients randomized to receive 300 mg, 6 of 25 secondary outcomes were statistically significant compared with placebo. Treatment-related adverse events occurred in 53.3% (16/30) of patients receiving 600 mg olamkicept, 58.1% (18/31) receiving 300 mg olamkicept, and 50% (15/30) receiving placebo. The most common drug-related adverse events were bilirubin presence in the urine, hyperuricemia, and increased aspartate aminotransferase levels, and all were more common in the olamkicept groups compared with placebo.

Conclusions and Relevance   Among patients with active ulcerative colitis, biweekly infusion of olamkicept 600 mg, but not 300 mg, resulted in a greater likelihood of clinical response at 12 weeks compared with placebo. Further research is needed for replication and to assess longer-term efficacy and safety.

Trial Registration   ClinicalTrials.gov Identifier: NCT03235752

Ulcerative colitis, one of the 2 major forms of inflammatory bowel disease, had an annual incidence of 8.8 to 23.1 per 100 000 person-years in North America and 0.97 to 57.9 per 100 000 person-years in Europe between 1990 and 2016. 1 The incidence of ulcerative colitis is increasing in countries such as China and Korea. 2 , 3 In China, it is anticipated that by 2035, there will be more than 2 million patients with ulcerative colitis, but few highly-effective therapies are available. 4 - 6 Ulcerative colitis is characterized by inflammatory pathophysiology and mucosal immune dysregulation, involving a dynamic, chronic activation of immune cells associated with increases in proinflammatory cytokines and intestinal mucosal injury. Many anticytokine therapies like anti-TNF therapy have significant adverse effects.

Interleukin 6 (IL-6), a pleiotropic proinflammatory cytokine, is a key mediator in chronic inflammation. Classic IL6 signaling is conveyed through the IL-6/IL-6R complex and 2 molecules of the signal transducer gp130. 7 Soluble IL-6R (sIL-6R), which originates from proteolytic cleavage of membrane-bound IL-6R, can form IL-6/sIL-6R complexes that convey IL-6 trans-signaling. 7 Sustained activation of IL-6 signaling triggers sIL-6R release, giving rise to IL-6 trans-signaling, 8 - 11 which is primarily responsible for chronic inflammation.

Olamkicept, a first-in-class, selective inhibitor of the sIL-6R/IL-6 complex, is a dimer formed by fusing 2 complete extracellular domains of gp130 to human IgG 1 Fc 12 , 13 that inhibits IL-6 trans-signaling by binding to and neutralizing the sIL-6R/IL-6 complexes but does not block classic IL-6 signaling. A phase 2a open-label trial (FUTURE) over 12 weeks in 16 patients with active Crohn disease or ulcerative colitis demonstrated distinct changes in mucosal pSTAT3 levels in biopsies from serial colonoscopies and was not associated with significant safety concern. 7

This phase 2 clinical trial was conducted to further investigate the effect of olamkicept in active ulcerative colitis.

This was an international, multicenter, randomized, double-blind, placebo-controlled phase 2b trial conducted between February 2018 and December 2020 at 22 clinical sites across mainland China, Taiwan, and South Korea. The trial protocol is reported in Supplement 1 . All patients provided written informed consent. The trial was conducted in accordance with the Declaration of Helsinki 14 and Good Clinical Practice standards, as described in the International Conference on Harmonization Guideline E6 (R2) and approved by study centers’ institutional review boards or ethics committees. A safety review committee reviewed the accumulating data regarding adverse events and provided recommendations to the sponsor on whether to continue, modify, or terminate the study.

The trial enrolled patients aged 18 to 70 years with confirmed ulcerative colitis for at least 3 months, who had active disease (total Mayo score ≥5, rectal bleeding score ≥1, and endoscopy score ≥2). The total Mayo score consists of 4 subscores: stool frequency, rectal bleeding, physician's global assessment, and endoscopic appearance. The full range for total Mayo score is 0 to 12, and each subscore ranges from 0 to 3, with a higher score indicating more severe disease. To be eligible, patients must have not responded to prior conventional nonbiological therapy and either had not received any biologic therapies or more than 8 weeks or 5 half-lives had elapsed since the last dose, whichever was longer. Conventional therapies, if still administered, were required at stable doses, with corticosteroids (≤20 mg/d prednisone or equivalent) for 2 or more weeks before randomization, 5-aminosalicylates-containing drugs (≥2 g/d 5-aminosalicylates) for at least 3 months and stable doses for 4 or more weeks before randomization, azathioprine (≥0.75 mg/kg/d) or 6-mercaptopurine (≥0.5 mg/kg/d) given for at least 6 months and stable doses for 6 or more weeks before randomization, and/or methotrexate at greater than or equal to 12.5 mg/week and stable doses for at least 12 weeks before randomization. Eligibility criteria are detailed in the full protocol ( Supplement 1 ).

Eligible patients were randomized 1:1:1 to receive olamkicept 600 mg or 300 mg or placebo. Central randomization was through a validated interactive web response system (Balance System) and stratified by current corticosteroid treatment (yes or no) and prior biologic treatment (yes or no). Treatment allocation was concealed so that treatment assignment was blinded from investigators, participants, and sponsors until the study was fully completed and the database was locked.

This study included a run-in period consisting of stable conventional treatments lasting up to 6 months’ duration (if stable conventional treatment was needed), a 4-week screening period for participants eligibility, a 12-week double-blind treatment period, and a 3-week follow-up for adverse events (to day 105) as described in eFigure 1 in Supplement 2 . Participants received placebo or olamkicept 600 or 300 mg by intravenous infusion at days 0, 14, 28, 42, 56, and 70. Participants were required to continue concomitant treatment with stable doses of corticosteroids, oral immunosuppressants, or 5-aminosalicylates during active treatment. Disease activity was assessed during screening, at baseline, and biweekly from week 2 to week 12 for partial Mayo score or for total Mayo score at weeks 0 and 12. All endoscopies were centrally read (1 reader at BioClinica Inc) with adjudication if results differed from the local reading.

Stool and blood samples were collected for laboratory testing, including assays for erythrocyte sedimentation rate and C-reactive protein. Other study procedures are detailed in the trial protocol in Supplement 1 .

The primary efficacy end point was clinical response at week 12 using the total Mayo score and defined as a decrease of 3 or greater and of 30% or greater from baseline in total Mayo score, including a decrease of at least 1 from baseline in rectal bleeding subscore or up to 1 in rectal bleeding subscore 15 with a primary comparison of olamkicept 600 mg or 300 mg vs placebo. 7 , 13 The primary safety outcome was the frequency of adverse events and serious adverse events.

Secondary efficacy end points included clinical remission per total Mayo score (defined as a total Mayo score ≤2, no individual subscore >1, and rectal bleeding subscore = 0); remission per modified Mayo score (defined as stool frequency subscore ≤1, rectal bleeding subscore = 0, and endoscopy subscore = 0 or 1) at week 12; mucosal healing (defined as endoscopic subscore = 0 or 1); change from baseline in total Mayo score and modified Mayo score at week 12; clinical response and remission defined per 9-point partial Mayo score at weeks 4, 6, 8, 10, and 12, changes from baseline in partial Mayo scores; and Physician’s Global Assessment at weeks 4, 6, 8,10 and 12.

Immunogenicity (anti-drug antibodies,such as Anti-TJ301 antibodies), pharmacokinetics (eAppendix 3 in Supplement 2 ), and biomarkers (erythrocyte sedimentation rate, C-reactive protein, IL-6, s-IL6R, IL-6/sIL-6R complex, neutrophil count, platelet count and fecal calprotectin) were secondary end points.

There were 4 versions of the protocol, and the study outcomes changed between the February 2017 version and the January 2020 version of the protocol. Investigators did not review any outcome data before changing the outcome measures ( Supplement 1 ).

A sample size of 27 patients per group was estimated to provide at least 70% power to detect a 30% increase in the 12-week clinical response rate between the placebo (assumed to be 30%) 16 and the treatment (assumed to be 60%) 7 group, with a 1-sided type I error rate of 0.05. This 30% increase in response was considered clinically meaningful given that a difference of greater than 20% has been considered as the minimal detectable difference. 16 - 18 Assuming a dropout rate of 10%, 30 patients were required per group.

The full analysis set included all randomized patients with at least 1 postbaseline 9-point partial Mayo score and was the primary analysis set for efficacy ( Supplement 3 ). The safety set included all patients who had received at least 1 dose of the study medication and had been evaluated for adverse events and laboratory abnormalities. All patients who discontinued treatment during the 12-week treatment period advanced to the trial end assessment visit, including endoscopy if consent was not withdrawn. Participants with missing data for a dichotomized end point, such as clinical response, clinical remission, and mucosal healing were classified as a nonresponder. Missing continuous end points, such as Mayo score and Physician’s Global Assessment change from baseline, were not imputed.

The primary end point was tested at the 1-sided .05 (2-sided .1) significance level based on the P value from the logistic regression model. The 90% CI for treatment comparison, which corresponded to the 1-sided .05 significance level, was provided. The statistical significance level and 90% CI were chosen because of the exploratory nature of this proof-of-concept phase 2 trial, designed to identify preliminary signals of efficacy to inform a decision about proceeding to a larger clinical trial. This exploratory clinical trial required a small but sufficient number of participants to infer whether there was an efficacy signal from the drug. Treatment comparison on secondary end points was not adjusted for multiplicity, and nominal P values were provided. Because of the potential for type I error due to multiple comparisons, findings for analyses of secondary end points should be interpreted as exploratory.

For dichotomized end points, point estimate, and 90% CI (to correspond with the 1-sided 0.05 significance level) were presented for each treatment group using the Clopper-Pearson method. This was a phase 2 trial designed to assess whether an efficacy signal existed. Therefore, a 90% CI was selected. The point estimate, 90% CI, and P value for comparisons of treatment with placebo were calculated using a logistic regression model with treatment group, randomization stratification factors, and baseline total Mayo score as covariates. Treatment comparison was further analyzed using the Cochran-Mantel-Haenszel test adjusted by stratification factors for sensitivity.

Continuous end points were analyzed using a mixed-effects model for repeated measures, with changes from baseline as the dependent variable, and baseline score, randomization stratification factor, treatment, visit, and treatment by visit interaction as fixed effects.

Prespecified subgroup analyses by time since initial diagnosis of ulcerative colitis (<7 or ≥7 years), baseline total Mayo score (≤8 or >8), corticosteroid treatment (yes or no), and prior biologic treatment (yes or no) were performed for efficacy end points. Post-hoc analyses were performed for subgroups that included age, sex, baseline partial Mayo score (≤7 or > 7) and baseline central endoscopy score (2 or 3).

All statistical analyses were performed with SAS version 9.4 (SAS Institute, Inc).

Between February 06, 2018, and December 16, 2020, there were 228 patients screened, and 91 eligible patients were randomly assigned to olamkicept 600 mg (n = 30), olamkicept 300 mg (n = 31), or placebo (n = 30) ( Figure 1 ). The dropout rate at 12-week follow-up was 10% (n = 3, olamkicept 600 mg), 6.5% (n = 2, olamkicept 300 mg) and 23.3% (n = 7, placebo). All participants were included in the safety analysis set, and the number of participants analyzed in the full analysis set was 29 for olamkicept 600 mg, 30 for olamkicept 300 mg, and 29 for placebo (among those in each group, 4, 3, and 8 had missing total Mayo score components at week 12 with 2, 2, and 6 missing partial Mayo score). At weeks 2, 4, 6, 8, and 10 where only partial Mayo score components measured, number of missing were 0, 2, 2, 2, and 2 in the olamkicept 600 mg group, 0, 1, 1, 1, and 1 in the olamkicept 300 mg group, and 0, 2, 5, 7, and 6 in the placebo group. The 3 groups were generally comparable in demographic and baseline characteristics ( Table 1 ).

In the full analysis set, significantly more patients receiving olamkicept 600 mg attained clinical response at week 12 than patients receiving placebo (58.6% [17/29] vs 34.5% [10/29]), with an adjusted difference of 26.6% (90% CI, 6.2% to 47.1%; P  = .03). Thirteen patients (43.3% [13/30]) receiving olamkicept 300 mg achieved clinical response at week 12, with no significant difference from placebo (adjusted difference, 8.3% [90% CI, −12.6% to 29.1%]; P  = .52) ( Figure 2 ).

Clinical remission based on the total Mayo score at week 12 occurred in 20.7% (6/29) of patients receiving olamkicept 600 mg and in 6.7% (2/30) of patients receiving olamkicept 300 mg but in no patients receiving placebo ( Figure 2 ), with a significant adjusted difference between olamkicept 600 mg and placebo (19.9% [90% CI, 12.5% to 27.3%]; P  < .001) and a nonstatistically significant adjusted difference between 300 mg and placebo (6.1% [90% CI, −0.8% to 12.9%]; P  = .14). Significantly more patients receiving olamkicept 600 mg (34.5% [10/29]) achieved mucosal healing at week 12 than patients receiving placebo (3.4% [1/29]), with an adjusted difference of 33.1% (90% CI, 18.3% to 47.9%; P  < .001) ( Figure 2 ). Additionally, 10% [3/30] patients receiving olamkicept 300 mg achieved mucosal healing at week 12 (adjusted difference vs placebo, 6.0% [90% CI, −4.4% to 16.3%]; P  = .34). Similar findings were noted in remission per modified Mayo score at week 12 ( Figure 2 ).

Compared with placebo, a significantly greater reduction of total Mayo score occurred in the olamkicept 600-mg group between baseline and 12-week follow-up (least square mean difference between olamkicept 600 mg and placebo, −1.6 [90% CI, −2.9 to −0.4]; P  = .03) ( Figure 3 A; eTable 1 in Supplement 2 ). The olamkicept 600-mg group was associated with a significant reduction in partial Mayo score compared with placebo at week 8 (least square mean difference, −1.0 [90% CI, −1.9 to 0.1]; P  = .08), week 10 (least square mean difference, −1.2 [90% CI, −2.0 to −0.3]; P  = .02), and week 12 (least square mean difference, −1.2 [90% CI, −2.1 to −0.2]; P  = .04). The olamkicept 300-mg group had a greater reduction in partial Mayo score at each visit than the placebo group, and the difference was statistically significant at week 8 (least square mean difference, −1.3 [90% CI, −2.2 to −0.4]; P  = .02) and at week 10 (least square mean difference, −1.1 [90% CI, −1.9 to −0.2]; P  = .04) ( Figure 3 B; eTable 1 in Supplement 2 ). The modified Mayo score in the olamkicept 600-mg group decreased from baseline at week 12 significantly more than the placebo group, (least square mean difference between olamkicept 600 mg and placebo, −1.4 [90% CI, −2.4 to −0.4]; P  = .02) ( Figure 3 C; eTable 1 in Supplement 2 ).

In the 600-mg olamkicept group, 16 of 25 secondary outcomes (specifically 8 of 9 outcomes at week 12 and 8 of 16 outcomes at weeks 4, 6, 8, and 10) were statistically significant, compared with placebo. For the 300-mg olamkicept group, 6 of 25 secondary outcomes (1 of 9 outcomes at week 12 and 5 of 16 at weeks 4, 6, 8, and 10) were statistically significant compared with placebo. (eTable 1 in Supplement 2 ).

Fecal calprotectin significantly declined between baseline and week 12 in patients receiving olamkicept 300 mg or 600 mg, but it increased in patients receiving placebo (eTable 2 and eFigure 3A in Supplement 2 ). Compared with placebo, there were no significant differences in mean changes from baseline in levels of neutrophil count, platelet count, erythrocyte sedimentation rate, C-reactive protein, IL-6, sIL-6Ra, and sIL-6R/IL-6 complex at 12-week follow-up between patients receiving olamkicept 300 mg or 600 mg and those receiving placebo (eTable 2, eFigures 3B, 3C, 3D, 3E, 3F, and eFigures 4E and 4F in Supplement 2 ).

Generally consistent treatment effects were observed across subgroups, with the overall analyses for the primary end point between patients receiving olamkicept 600 mg and those receiving placebo (eFigure 2 in Supplement 2 ).

80.0% of patients in the olamkicept 600-mg group, 87.1% in the olamkicept 300-mg group, and 66.7% in the placebo group received all 6 doses. The median drug exposure duration was 71 days in all 3 groups. One patient receiving olamkicept 600 mg and 1 patient receiving placebo withdrew due to adverse events, and treatment was temporarily discontinued due to adverse events in 1 patient receiving olamkicept 600 mg.

Adverse events occurred in 83.3% (25/30) of patients in the olamkicept 600-mg group, 93.5% (29/31) in the olamkicept 300-mg group, and 90% (27/30) in the placebo group, and serious adverse events in occurred in 3.3% (1/30) of patients in the olamkicept 600-mg group, 3.2% (1/31) in the olamkicept 300-mg group, and 6.7% (2/30) in the placebo group ( Table 2 ). All serious adverse events resolved after treatment. Treatment-related adverse events occurred in 53.3% (16/30) of patients in the olamkicept 600-mg group, 58.1% (18/31) in the olamkicept 300-mg group, and 50% (15/30) in the placebo group. No patients died.

The most common (≥5%) drug-related adverse events in the treatment group with a higher incidence rate than the placebo group were bilirubin presence in the urine (6.7% in patients receiving 600 mg olamkicept, 16.1% in patients receiving 300 mg olamkicept, and 10.0% in patients receiving placebo), hyperuricemia (6.7% in patients receiving 600 mg olamkicept, 9.7% in patients receiving 300 mg olamkicept, and 3.3% in patients receiving placebo), and increased serum aspartate aminotransferase (3.3% in patients receiving 600 mg olamkicept, 9.7% in patients receiving 300 mg olamkicept, and 0 in patients receiving placebo). No significant differences were observed in changes in platelet count and neutrophil count at weeks 4 to 12 from baseline between patients receiving olamkicept 600 mg and those receiving placebo (eFigure 4E and 4F in Supplement 2 ). A total of 7 patients who received olamkicept reported 7 adverse events of special interest, including a positive interferon-gamma release assay in 5 patients (8.2% [with 1 {3.3%} in the 600-mg olamkicept group and 4 {12.9%} in the 300-mg olamkicept group]), aspartate aminotransferase increased in 1 patient (3.2%) in the 300-mg olamkicept group, and hypersensitivity reaction in 1 patient (3.3%) in the 600-mg olamkicept group. No tuberculosis infection was diagnosed based on further evaluation of the positive interferon-gamma release assay test.

Olamkicept plasma concentrations showed similar decline over time in both olamkicept groups (eFigure 5A and eTable 3 in Supplement 2 ), and the trough plasma concentrations remained stable (eFigure 5B in Supplement 2 ). Following the first dose, the exposure of olamkicept increased dose proportionally with a geometric mean of C max being 77.8 μg/mL with 300 mg olamkicept and 159.7 μg/mL with 600 mg olamkicept. Following multiple doses of olamkicept 600 mg (sixth dose), the geometric mean of half-life was 3.4 days, steady state apparent clearance was 0.126 L/hour, and apparent volume of distribution was 14.7 L.

One patient (3.3%) receiving olamkicept 600 mg and 5 patients (16.1%) receiving olamkicept 300 mg developed antidrug antibodies (eTable 4 in Supplement 2 ).

Among patients with active ulcerative colitis, biweekly infusion of olamkicept 600 mg, but not 300 mg, resulted in a significantly higher rate of clinical response at 12 weeks compared with placebo. Olamkicept improved 8 of 9 secondary efficacy outcomes measured at week 12 (including clinical remission and mucosal healing) compared with placebo, using the 1-sided P value of .05. Patients with a baseline Mayo score greater than 8 or endoscopic score of 3 had lower response rates to olamkicept 600 mg compared with others who did not have these characteristics. Compared with placebo, there was a higher incidence of bilirubin in urine, hyperuricemia, and elevated aspartate aminotransferase in patients randomized to the olamkicept treatment group. Further study in a larger sample size is needed to evaluate the higher rates of these adverse events.

Serum olamkicept concentration increased dose-dependently, and olamkicept 600 mg reached a steady state after 4 weeks of biweekly administration, without obvious accumulation. Additionally, the rate of antidrug antibodies was low for olamkicept, as expected for fusion proteins like etanercept, and had no effect on efficacy and safety. 19 , 20

This study had several limitations. First, only 5.5% of participants had prior exposure to biologic therapies, suggesting that the participant population did not have severe ulcerative colitis. Second, the sample size was small. Third, the trial used 90% CIs, consistent with a 1-sided type I error rate of .05 in reporting given the exploratory nature of this phase 2 study. Fourth, the drop-out rate was 23.3% in the placebo group, a rate that was substantially higher than in the 600 mg (10.0%) and 300 mg (6.5%) olamkicept groups. Fifth, additional clinical trials are required to prove efficacy in induction and maintenance therapy and further evaluate potentially important adverse events.

Among patients with active ulcerative colitis, biweekly infusion of olamkicept 600 mg, but not 300 mg, resulted in a greater likelihood of clinical response at 12 weeks compared with placebo. Further research is needed for replication and to assess longer-term efficacy and safety.

Corresponding Author: Minhu Chen, MD, Department of Gastroenterology, The First Affiliated Hospital, Sun Yat-Sen University, 58 Zhongshan Rd 2, 510080 Guangzhou, PR China ( [email protected] ).

Accepted for Publication: January 25, 2023.

Author Contributions: Drs Shenghong Zhang and Minhu Chen had full access to all of the data in the study and take responsibility for the integrity of the data and the accuracy of the data analysis. Drs Shenghong Zhang and Baili Chen contributed equally to this work.

Concept and design: Shenghong Zhang, B. Chen, B. Wang, Cao, Zhong, Shieh, Ran, Q. Wang, Su Zhang, Schreiber, M. Chen.

Acquisition, analysis, or interpretation of data: Shenghong Zhang, B. Chen, B. Wang, H. Chen, Li, Cao, Zhong, Tang, Yang, Xu, Q. Wang, Liu, Ma, X. Wang, N. Zhang, Su Zhang, Guo, Huang, Schreiber, M. Chen.

Drafting of the manuscript: Shenghong Zhang, B. Chen, B. Wang, Cao, Yang, Liu, Ma, X. Wang, N. Zhang, Huang, Schreiber, M. Chen.

Critical revision of the manuscript for important intellectual content: Shenghong Zhang, B. Chen, B. Wang, H. Chen, Li, Cao, Zhong, Shieh, Ran, Tang, Xu, Q. Wang, Liu, N. Zhang, Su Zhang, Guo, Huang, Schreiber, M. Chen.

Statistical analysis: Shenghong Zhang, B. Chen, B. Wang, Cao, Yang, Q. Wang, N. Zhang, M. Chen.

Obtained funding: M. Chen.

Administrative, technical, or material support: H. Chen, Shieh, Yang, Liu, Ma, X. Wang, Huang, Schreiber, M. Chen.

Supervision: Shenghong Zhang, B. Chen, B. Wang, H. Chen, Li, Zhong, Ran, Tang, Yang, Su Zhang, Guo, M. Chen.

Other - Results analysis, discussion with investigators (as the study physician of I-Mab): Xu.

Conflict of Interest Disclosures: Dr Shenghong Zhang reported personal fees (for consulting) from I-Mab Biopharma during the conduct of the study; and personal fees (for lectures) from Takeda, AbbVie, Abbott, and Janssen outside the submitted work. Dr B. Chen reported personal fees (for consulting) from I-Mab Biopharma during the conduct of the study; and personal fees (for lectures) from Takeda, AbbVie, Abbott, and Janssen outside the submitted work. Dr H. Chen reported personal fees (for lectures) from Janssen, Takeda, AbbVie, and Abbott outside the submitted work. Dr Li reported personal fees (for lectures) from Janssen, Takeda, AbbVie, and Abbott outside the submitted work. Dr Tang reported personal fees from I-Mab Biopharma during the conduct of the study; and personal fees from Takeda outside the submitted work. Ms Yang reported being an employee of I-Mab Biopharma and stock ownership with I-Mab Biopharma. Dr Xu reported being an employee of I-Mab Biopharma and stock ownership with I-Mab Biopharma. Dr Q. Wang reported being an employee of I-Mab Biopharma and stock ownership with I-Mab Biopharma. Dr Liu reported being an employee of I-Mab Biopharma and stock ownership with I-Mab Biopharma. Dr Ma reported stock ownership with I-Mab Biopharma during the conduct of the study. Dr Schreiber reported personal fees (for consulting) from Ferring and from I-Mab (lecture fees) during the conduct of the study; personal fees (lectures and/or consulting) from Abbvie, Amgen, Biogen, Bristol Myers Squibb, Falk, Galapagos, Gilead, Hikma, MSD, Pfizer, Janssen, and Takeda outside the submitted work. Dr M. Chen reported personal fees (for advisory functions) from I-Mab Biopharma and grants from National Key S&T Special Project during the conduct of the study; and personal fees (for lectures) from Takeda, AbbVie, and Janssen outside the submitted work. No other disclosures were reported.

Funding/Support: This study was sponsored by I-Mab Biopharma. This work was funded by I-Mab Biopharma Hong Kong Limited and National Key S&T Special Project (2018ZX09301-013).

Role of the Funder/Sponsor: The trial was designed by the investigators and I-Mab Biopharma. I-Mab Biopharma had an oversight role in the conduct of the study and collection, analysis, and interpretation of the data. I-Mab Biopharma had the right to review the manuscript but did not have the right to veto publication or control the decision regarding to which journal the manuscript was submitted, and several individuals employed by I-Mab Biopharma were coauthors of the manuscript who fulfilled authorship criteria. All decisions regarding publication of the study results were made by the academic steering committee and approved by all authors.

Data Sharing Statement: See Supplement 4 .

Additional Contributions: We thank the patients and the study staff who participated in this trial. We thank all the participating investigational sites and the principal investigators at these sites who participated in this study: Minhu Chen, The First Affiliated Hospital, Sun Yat-sen University, China; Bangmao Wang, General Hospital, Tianjin Medical University, China; Hong Chen, Affiliated ZhongDa Hospital, School of Medicine, Southeast University, China; Yan Li, Shengjing Hospital of China Medical University, China; Quian Cao, Sir Run Run Shaw Hospital, Zhejiang University, China; Jie Zhong, Ruijin Hospital, Shanghai Jiaotong University School of Medicine, China; Zhonghui Wen, West China Hospital of Sichuan University, China; Ming-Jium Shieh, National Taiwan University Hospital & College of Medicine, Taiwan, China; Hongjie Zhang, Jiangsu Province Hospital, China; Zhihua Ran, Renji Hospital, Shanghai Jiaotong University School of Medicine, China; Tongyu Tang, Bethune First Affiliated Hospital of Jilin University, China; Xiang Gao, The Sixth Affiliated Hospital of Sun Yat-sen University, China; Wensong Ge, Xinhua Hospital affiliated to Shanghai Jiao Tong University School of Medicine, China; Qi Wang, Second Hospital of Shanxi Medical University, China; Youxiang Chen, The First Affiliated Hospital of Nanchang University, China; Weihong Sha, Guangdong Provincial People's Hospital, China; Side Liu, Nanfang Hospital, China; Cheng-Tang Chiu, Chang Gung Memorial Hospital-Linkou, Taiwan, China; Hong Wei, Hainan General Hospital, China; Xiaoping Zou, Nanjing Drum Tower Hospital; China; Byung Ik Jang, Yeungnam University Medical Center, South Korea; Jianqiu Sheng, The Seventh Medical Center of Chinese PLA General Hospital, China.

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• Systematic Review
• Open access
• Published: 19 August 2024

Efficacy and safety of second-line therapies for advanced hepatocellular carcinoma: a network meta-analysis of randomized controlled trials

• Fenping Lu 1 , 2   na1 ,
• Kai Zhao 3   na1 ,
• Miaoqing Ye 4 ,
• Guangyan Xing 1 , 2 ,
• Bowen Liu 1 , 2 ,
• Xiaobin Li 1 , 2 ,
• Yun Ran 2 ,
• Fenfang Wu 2 ,
• Wei Chen 5 &
• Shiping Hu 2  

BMC Cancer volume  24 , Article number:  1023 ( 2024 ) Cite this article

234 Accesses

Metrics details

The selection of appropriate second-line therapy for liver cancer after first-line treatment failure poses a significant clinical challenge due to the lack of direct comparative studies and standard treatment protocols. A network meta-analysis (NMA) provides a robust method to systematically evaluate the clinical outcomes and adverse effects of various second-line treatments for hepatocellular carcinoma (HCC).

We systematically searched PubMed, Embase, Web of Science and the Cochrane Library to identify phase III/IV randomized controlled trials (RCTs) published up to March 11, 2024. The outcomes extracted were median overall survival (OS), median progression-free survival (PFS), time to disease progression (TTP), disease control rate (DCR), objective response rate (ORR), and adverse reactions. This study was registered in the Prospective Register of Systematic Reviews (CRD42023427843) to ensure transparency, novelty, and reliability.

We included 16 RCTs involving 7,005 patients and 10 second-line treatments. For advanced HCC patients, regorafenib (HR = 0.62, 95%CI: 0.53–0.73) and cabozantinib (HR = 0.74, 95%CI: 0.63–0.85) provided the best OS benefits compared to placebo. Cabozantinib (HR = 0.42, 95%CI: 0.32–0.55) and regorafenib (HR = 0.46, 95% CI: 0.31–0.68) also offered the most significant PFS benefits. For TTP, apatinib (HR = 0.43, 95% CI: 0.33–0.57), ramucirumab (HR = 0.44, 95% CI: 0.34–0.57), and regorafenib (HR = 0.44, 95% CI: 0.38–0.51) showed significant benefits over placebo. Regarding ORR, ramucirumab (OR = 9.90, 95% CI: 3.40–42.98) and S-1 (OR = 8.68, 95% CI: 1.4–154.68) showed the most significant increases over placebo. Apatinib (OR = 3.88, 95% CI: 2.48–6.10) and cabozantinib (OR = 3.53, 95% CI: 2.54–4.90) provided the best DCR benefits compared to placebo. Tivantinib showed the most significant advantages in terms of three different safety outcome measures.

Conclusions

Our findings suggest that, in terms of overall efficacy and safety, regorafenib and cabozantinib are the optimal second-line treatment options for patients with advanced HCC.

Peer Review reports

Introduction

Hepatocellular carcinoma (HCC) is the sixth most prevalent cancer globally and the third leading cause of cancer-related mortality. World Health Organization (WHO) projections indicate that liver cancer incidence will increase by 55.0% between 2020 and 2040, leading to an estimated 1.3 million deaths. This represents a significant 56.4% rise from 2020 statistics [ 1 ].

HCC is the predominant subtype of liver cancer, accounting for approximately 90% of cases [ 2 ]. Primary treatments for early-stage HCC include liver resection, transplantation, and radiofrequency ablation [ 3 ]. However, due to the lack of early clinical symptoms, over 50% of cases are diagnosed at an advanced stage, making surgical interventions unsuitable [ 4 ]. Immune checkpoint inhibitors (ICIs), tyrosine kinase inhibitors (TKIs), and monoclonal antibodies are now the primary treatments for advanced liver cancer, enhancing patient survival and quality of life [ 5 ].

In first-line treatment, immunotherapy and immune-based combinations (paired with TKIs or anti-angiogenic drugs, among others) have emerged as one of the most promising therapeutic strategies evaluated in recent years [ 6 , 7 ]. However, due to the significant heterogeneity of liver cancer, the susceptibility to resistance of multi-kinase target drugs, and the adverse reactions of ICIs (such as elevated transaminase levels) [ 8 , 9 ], disease progression and recurrence can occur post-initial treatment, leading to multiple second-line treatment recommendations in guidelines [ 10 ]. Second-line treatments include targeted therapies (e.g., sorafenib, lenvatinib), immunotherapies (e.g., nivolumab, pembrolizumab), radioembolization with Yttrium-90, chemotherapeutic agents (e.g., cabozantinib, regorafenib), or participation in clinical trials for novel therapies [ 11 , 12 ]. These treatments aim to target various aspects of cancer cells or the tumor microenvironment to manage the disease and improve patient outcomes. However, clinical guidelines lack consensus on second-line treatments for liver cancer due to limited evidence post-sorafenib failure and insufficient high-level evidence for new first-line regimens [ 13 , 14 ].

With the increasing number of randomized controlled trials (RCTs), most compare second-line treatments against placebo. Therefore, establishing optimal second-line treatment strategies is crucial for designing future head-to-head clinical studies. To address this, we have integrated data from several large phase III clinical trials to perform indirect comparisons of key outcomes, including overall survival (OS), progression-free survival (PFS), objective response rate (ORR), disease control rate (DCR), time to progression (TTP), adverse events (AEs), incidence of grade 3-4AEs, and treatment discontinuations. This network meta-analysis (NMA) of second-line treatments aims to provide valuable insights into their effectiveness, thereby aiding in clinical decision-making for liver cancer treatment.

This NMA adhered to the guidelines outlined in the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) extension statement [ 15 ]. The study protocol has been registered in the Prospective Register of Systematic Reviews (CRD42023427843) to ensure transparency, reliability, and novelty.

Literature search

The search was conducted across databases, including PubMed, Embase, Web of Science, and the Cochrane Library. Additional manual searches of references were performed to prevent any oversights. The search terms utilized were "hepatocarcinoma," "hepatocellular carcinoma," "second-line," "immunotherapy," and "targeted therapy." The search period spans from the inception of each database to March 10, 2024. The details of all search strategies employed for the four targeted databases are presented in Table S1 , following the completion of the electronic search.

Inclusion and exclusion criteria

Inclusion criteria.

All clinical studies included in the analysis adhered to the PICOS criteria [ 16 ]:

1) Patients aged 18 years or older with advanced HCC who have received first-line treatments.

2) Patients who received a second-line treatment in phase III/IV prospective RCTs.

3) Comparator options included systemic therapy, placebo, or best supportive care.

4) Prognoses included at least one of the following components: OS, PFS, TTP, ORR, DCR, the rate of all grade and grade 3-4AEs, and the rate of treatment discontinuation due to AEs.

5) Publications were restricted to those in English.

Exclusion criteria

1) Duplicated publications.

2) Inability to fully obtain outcome measures (e.g., some outcome measures not reported using mean and variance or data errors).

Literature selection

Two researchers independently screened literature titles and abstracts based on inclusion and exclusion criteria, excluding studies that did not meet the criteria. Full-text screening was then conducted to select studies for inclusion. EndNote software was used for literature management, and an Excel spreadsheet was created to extract data. In cases of disagreement during screening, a third researcher assessed the studies, and consensus was reached through discussion.

Data extraction

Extracted data included:

1) Basic information of the clinical trial, including authorship, publication date, and clinical trial registration number.

2) Study design of the clinical trial, including sample size, allocation, intervention model, masking, and primary purpose.

3) Basic characteristics of included patients, including gender ratio, median age, and baseline liver condition.

4) Treatments of the experimental and control groups.

5) Outcomes of the study, including PFS, OS, ORR, DCR, the rate of all grade and grade 3-4AEs, and the rate of treatment discontinuation due to AEs.

Quality assessment

According to the Cochrane Handbook version 5.1.0, the quality of included studies was assessed using recommended tools for evaluating bias risk. This assessment covered random sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, completeness of data, selective outcome reporting, and other biases. The risk levels for the included RCT studies were categorized as low risk, high risk, and unclear.

Statistical analysis

The primary endpoints were OS, PFS, TTP, ORR, and DCR. The secondary endpoints included all-grade and grade 3–4 AEs and the rate of treatment discontinuation due to AEs. Hazard ratios (HRs) with 95% confidence intervals (CIs) were used as effect measures for OS, PFS, and TTP, while odds ratios (ORs) with 95% CIs were used for ORR, DCR, all-grade and grade 3–4 AEs, and the rate of treatment discontinuation due to AEs.

NMA was conducted within a Bayesian framework using the "rjags" and "gemtc" packages in R software to evaluate the efficacy and safety of second-line therapies for advanced HCC. A fixed-effects model was employed to establish three independent Markov chains, each running 20,000 burn-in iterations followed by 50,000 sampling iterations. The iteration results of the Markov chains, represented as HRs and ORs, were used to rank the efficacy and safety of the different treatment regimens, with the findings visualized through graphical representations. Publication bias was assessed using funnel plots.

Study selection

Preliminary retrieval yielded 597 relevant articles, of which 263 remained after deduplication. Following screening of titles and abstracts to exclude review articles, experimental studies, and conference papers, 160 articles were retained. After full-text review and adherence to inclusion and exclusion criteria, a total of 16 articles were included [ 17 , 18 , 19 , 20 , 21 , 22 , 23 , 24 , 25 , 26 , 27 , 28 , 29 , 30 , 31 , 32 ]. Finally, the study involved a total of 7,005 participants, with 4,573 in the experimental group and 2,432 in the control group. The literature screening process is depicted in Fig.  1 .

Flowchart of study identification and selection process

Study and characteristics

All included studies were prospective, phase III clinical RCTs. A total of 11 studies were multi-center, 2 were conducted in mainland China, and of the remaining trials, 2 were in USA and 1 in Japan. The drugs tested in the active treatments were pembrolizumab (2), ramucirumab (3), apatinib (1), cabozantinib (2), tivantinib (2), regorafenib (2), ADI-PEG20 (1), S-1 (1), everolimus (1), brivanib (1). The included populations were not discernibly different. The results of the risk of bias are provided in Fig.  2 . No trials directly compared different active treatments, and detailed characteristics of the included studies are presented in Table  1 .

The risk of bias of included studies. A Methodological quality summary: authors’ judgment about each methodological quality item for each included study. Performance bias and detection bias presented were for risk of bias; ( B ) Methodological quality graph: authors’ judgment about each methodological quality item presented as percentages across all included studies

Network meta -analyses

Comparisons of os, pfs.

The primary outcomes of this study were OS and PFS. The NMA included 10 second-line treatment regimens reporting OS (Fig.  3 A) and 8 regimens reporting PFS (Fig.  3 B) for patients with HCC.

Network diagram comparing the efficacy of various second-line treatments in patients with advanced HCC. Comparisons were generated using the Bayesian framework on ( A ) OS ( B ) PFS ( C ) TTP ( D ) ORR

Regarding OS, 16 studies were included, encompassing a total of 10 different treatment regimens: pembrolizumab (2), everolimus (1), brivanib (1), apatinib (1), cabozantinib (2), ADI-PEG20 (1), tivantinib (2), S-1 (1), regorafenib (2),and ramucirumab (3). Due to the lack of a closed-loop structure, a consistency model was used.

Compared to the placebo group, regorafenib (HR = 0.62, 95% CI: 0.53–0.73) provided the best OS benefit, followed by cabozantinib (HR = 0.74, 95% CI: 0.63–0.85), apatinib (HR = 0.78, 95% CI: 0.62–1.00), and pembrolizumab (HR = 0.79, 95% CI: 0.67–0.93). Everolimus (HR = 1.05, 95% CI: 0.86–1.27) was the only second-line treatment that did not show an OS benefit compared to placebo (Fig.  4 A).

League table of the efficacy of various second-line treatments for advanced HCC based on Bayesian network meta-analysis. ( A )OS ( B )PFS. An HR < 1.00 indicates better survival benefits

Regarding PFS, 13 studies were included, encompassing a total of 8 different treatment regimens: pembrolizumab (2), apatinib (1), cabozantinib (2), ADI-PEG20 (1), tivantinib (2), S-1 (1), regorafenib (2), and ramucirumab (3). Due to the lack of a closed-loop structure, a consistency model was used.

Almost all second-line treatments provided better PFS compared to the placebo group, with the sole exception being ADI-PEG20 (HR = 1.17, 95% CI: 0.80–1.72), which showed the least PFS benefit among all treatments. Among second-line treatments, cabozantinib (HR = 0.42, 95% CI: 0.32–0.55) and regorafenib (HR = 0.46, 95% CI: 0.31–0.68) offered the greatest PFS benefits compared to placebo, followed by apatinib (HR = 0.47, 95% CI: 0.32–0.70), ramucirumab (HR = 0.55, 95% CI: 0.42–0.69), and S-1 (HR = 0.60, 95% CI: 0.40–0.90). Additionally, pembrolizumab (HR = 0.73, 95% CI: 0.55–0.69) also provided significant PFS benefits compared to placebo (Fig.  4 B).

Comparisons of TTP, ORR and DCR

The secondary outcomes of this study were TTP, ORR, and DCR. The NMA included 7 second-line treatment regimens for TTP (Fig.  3 C), 8 for ORR (Fig.  3 D), and 9 for DCR (Fig.  5 A) in patients with HCC.

Network diagram comparing the efficacy of various second-line treatments in patients with advanced HCC. Comparisons were generated using the Bayesian framework on ( A ) DCR ( B ) Any grade AEs ( C ) Grade3-4 AEs ( D ) AEs requiring treatment discontinuation

Regarding TTP, 10 studies were included, encompassing a total of 7 different treatment regimens: everolimus (1), brivanib (1), apatinib (1), tivantinib (1), S-1 (1), regorafenib (2), and ramucirumab (3). Due to the lack of a closed-loop structure, a consistency model was used.

All second-line treatments showed benefits compared to the placebo group. Apatinib (HR = 0.43, 95% CI: 0.33–0.57), ramucirumab (HR = 0.44, 95% CI: 0.34–0.57), regorafenib (HR = 0.44, 95% CI: 0.38–0.51), brivanib (HR = 0.56, 95% CI: 0.42–0.75), and S-1 (HR = 0.59, 95% CI: 0.46–0.76) provided significant benefits compared to the placebo group. Further comparisons of the active interventions suggest that apatinib (HR = 0.47, 95% CI: 0.33–0.65) and brivanib (HR = 0.60, 95% CI: 0.42–0.87) are superior to everolimus and tivantinib. Ramucirumab (HR = 0.46, 95% CI: 0.32–0.67), regorafenib (HR = 0.46, 95% CI: 0.34–0.62), and S-1 (HR = 0.61, 95% CI: 0.43–0.88) are also superior to tivantinib (Fig.  6 C).

League table of the efficacy of various second-line treatments for advanced HCC based on BayesianNMA. (C)TTP (D)ORR (E)DCR. An HR < 1.00 indicates better survival benefits. An OR > 1.00 indicates better efficacy

Regarding ORR, 12 studies were included, encompassing a total of 8 different treatment regimens: cabozantinib (2), apatinib (1), tivantinib (1), brivanib (1), S-1 (1), regorafenib (1), ramucirumab (3), and pembrolizumab (2). Due to the lack of a closed-loop structure, a consistency model was used.

Except for tivantinib (OR = 0.46, 95% CI: 0.01–17.43), all second-line treatments significantly improved ORR compared to the placebo group. Ramucirumab (OR = 9.90, 95% CI: 3.4–42.98), S-1 (OR = 8.68, 95% CI: 1.40–154.68), and cabozantinib (OR = 6.95, 95% CI: 2.40–31.31) showed the most significant improvements compared to placebo. Pembrolizumab (OR = 6.92, 95% CI: 3.47–15.86), apatinib (OR = 5.92, 95% CI: 2.00–27.35), and brivanib (OR = 5.23, 95% CI: 1.71–24.27) also showed considerable improvements compared to placebo (Fig.  6 D).

Regarding DCR, 12 studies were included, covering 9 different treatment regimens: pembrolizumab (2), everolimus (1), cabozantinib (1), brivanib (1), apatinib (1), tivantinib (1), S-1 (1), regorafenib (1), and ramucirumab (3). Due to the lack of a closed-loop structure, a consistency model was used.

For DCR, all second-line treatments showed significant improvements compared to the placebo group, except for tivantinib (OR = 0.98, 95% CI: 0.62–1.54). Apatinib (OR = 3.88, 95% CI: 2.48–6.10), cabozantinib (OR = 3.53, 95% CI: 2.54–4.90), and regorafenib (OR = 3.31, 95% CI: 2.32–4.79) provided the best DCR benefits compared to the placebo group. S-1 (OR = 2.39, 95% CI: 1.46–4.05) and brivanib (OR = 2.32, 95% CI: 1.50–3.58) also showed significant DCR advantages compared to placebo (Fig.  6 E).

Safety and toxicity

To evaluate the safety and toxicity across studies, we assessed the rate of all-grade and grade 3–4 AEs and the rate of treatment discontinuation due to AEs. The NMA included 10 second-line treatment regimens reporting AEs (Fig.  5 B), 9 regimens reporting grade 3–4 AEs (Fig.  5 C), and 8 regimens reporting the rate of treatment discontinuation due to AEs (Fig.  5 D) in patients with HCC.

Regarding any grade AEs, 12 studies were included, covering 9 different treatment regimens: pembrolizumab (2), everolimus (1), cabozantinib (1), brivanib (1), apatinib (1), tivantinib (2), S-1 (1), regorafenib (1), and ramucirumab (2). All second-line treatments had higher AE incidence rates compared to the placebo group. Among these treatments, tivantinib (OR = 1.23, 95% CI: 0.19–7.41), pembrolizumab (OR = 2.41, 95% CI: 0.44–15.73), and cabozantinib (OR = 3.83, 95% CI: 0.31–48.53) had relatively lower AE incidence rates, which were not statistically significant compared to placebo (Fig.  7 F).

League table of the safety of various second-line treatments for advanced HCC based on Bayesian NMA. F Any grade AEs ( G ) grade3-4 adverse events ( H ) AEs requiring treatment discontinuation. An OR < 1.00 indicates better safety

Regarding grade 3–4 AEs, 12 studies were included, covering 8 different treatment regimens: pembrolizumab (2), everolimus (1), cabozantinib (1), brivanib (1), apatinib (1), tivantinib (1), regorafenib (2), and ramucirumab (3). All second-line treatments had higher grade 3–4 AE incidence rates compared to the placebo group. Among these treatments, tivantinib (OR = 1.00, 95% CI: 0.18–5.34) and ramucirumab (OR = 1.95, 95% CI: 0.96–10.82) had relatively lower incidence rates of grade 3–4 AEs, which were not statistically significant compared to placebo (Fig.  7 G).

Regarding AEs requiring treatment discontinuation, 10 studies were included, covering 7 different treatment regimens: pembrolizumab (2), everolimus (1), cabozantinib (1), apatinib (1), tivantinib (1), regorafenib (1), and ramucirumab (3). All second-line treatments had higher incidence rates of AEs requiring treatment discontinuation compared to the placebo group. Among these treatments, tivantinib (OR = 1.33, 95% CI: 0.65–2.89) and regorafenib (OR = 1.41, 95% CI: 0.92–2.18) had relatively lower incidence rates of AEs requiring treatment discontinuation, which were not statistically significant compared to placebo (Fig.  7 H).

Ranking analysis was conducted based on Bayesian ranking profiles. For all efficacy assessment indicators in advanced HCC patients, regorafenib is most likely to rank first in OS with a cumulative probability of 98.06%, followed by cabozantinib (80.19%) and pembrolizumab (68.06%). Cabozantinib has the highest probability of ranking first in PFS (90.52%), followed by regorafenib (81.38%) and apatinib (78.54%). In ORR, ramucirumab has the highest probability of ranking first (77.67%), followed by S-1 (70.95%), pembrolizumab (66.59%), and cabozantinib (66.46%). In DCR, apatinib is most likely to rank first (91.04%), followed by cabozantinib (86.76%) and regorafenib (82.67%). In TTP, apatinib is most likely to rank first (84.93%), followed by regorafenib (83.90%) and ramucirumab (82.08%).

For all safety and toxicity assessment indicators, regarding any grade AEs, excluding the placebo group, tivantinib is most likely to rank first (85.35%), followed by pembrolizumab (69.14%) and cabozantinib (56.81%). For grade 3-4AEs, excluding the placebo group, tivantinib is most likely to rank first (85.77%), followed by pembrolizumab (67.15%) and ramucirumab (57.25%). For AEs requiring treatment discontinuation, excluding the placebo group, tivantinib ranks first (77.81%), regorafenib ranks second (75.24%), and pembrolizumab ranks third (58.00%) (Fig. S1 –7).

Heterogeneity and inconsistency

Publication bias analysis was conducted using funnel plots for six different outcome indicators. The results indicated that the scatter plot distribution of the studies was symmetrical, with no scattered distribution of study points, suggesting a low likelihood of publication bias in this study (Fig. S9, S10). The pairwise meta-analysis results based on frequentist methods were consistent with the corresponding pooled results from the Bayesian framework (Fig. S11). Heterogeneity was assessed using the Q-test and I 2 statistic. Results showed that if I 2  = 0% or I 2  ≤ 50%, indicating low heterogeneity, a fixed-effects model was used. If I 2  > 50%, indicating heterogeneity, a random-effects model was used.

Our study provides evidence-based support for clinical practice, including the following findings:

1) Almost all second-line treatments provided survival advantages over the placebo group in terms of OS, PFS, ORR, TTP, and DCR.

2) None of the second-line treatments showed safety or toxicity advantages over the placebo group.

3) For advanced HCC patients, regorafenib has the highest probability of providing the best OS among second-line treatments, cabozantinib has the highest probability of providing the best PFS, ramucirumab ranks highest in ORR, and apatinib ranks highest in both DCR and TTP.

4) For advanced HCC patients, tivantinib has the highest probability of ranking first in any grade AEs, grade 3–4 AEs, and AEs requiring treatment discontinuation among second-line treatments.

5) Regorafenib shows a good balance of efficacy and safety, ranking first in OS, second in PFS, third in DCR, second in TTP, and second in AEs requiring treatment discontinuation. Cabozantinib also shows excellent efficacy and safety, ranking second in OS, first in PFS, second in DCR, fourth in ORR, and third in any grade AEs. Regorafenib, cabozantinib, and ramucirumab have very similar HRs for OS. Upon further analysis, it was found that a higher proportion of patients in the ramucirumab trial had alpha-fetoprotein (AFP) levels above 400 ng/mL, indicating more aggressive and rapidly progressing disease. This may explain why the HR for OS in the ramucirumab trial is not as favorable as those for regorafenib and cabozantinib. In the regorafenib trial, patients had to tolerate 400 mg of sorafenib for at least 72% of the time during first-line treatment before progressing to second-line treatment with regorafenib. This restriction was not present in the cabozantinib trial. Based on our study results, cabozantinib should be prioritized for advanced HCC patients who do not meet this criterion, while regorafenib should be chosen for those who do.

In addition to targeted therapies, our study also included the PD-1 inhibitor pembrolizumab as a second-line treatment. Pembrolizumab demonstrated significant OS benefits compared to placebo (HR = 0.79, 95% CI: 0.67–0.93) and ranked second in safety, just behind tivantinib. PD-1 inhibitors block the interaction between PD-1 and its ligands PD-L1 and PD-L2, thereby inhibiting immune escape. Unlike traditional chemotherapy, these inhibitors have a selective immune function, which explains why pembrolizumab shows substantial OS benefits while maintaining relatively good safety. A NMA by Lei et al. evaluated the effectiveness and safety of ICIs as a primary treatment for unresectable liver cancer. Their findings support the higher survival rates of patients receiving ICI-based treatments when treatment-related AEs are tolerable. This further corroborates the excellent performance of pembrolizumab in our study [ 33 ].

Previous NMAs focused on the efficacy and safety of second-line treatments for advanced HCC, limited to patients resistant to or progressing after sorafenib [ 34 , 35 ]. In 2020, Wang et al. compared only four second-line treatment drugs (pembrolizumab, ramucirumab, cabozantinib, and regorafenib), indicating that regorafenib and cabozantinib improved OS in patients with HCC [ 34 ].  In 2022, Solimando AG et al. demonstrated through their NMA that regorafenib, cabozantinib, and ramucirumab significantly extended OS in patients. Additionally, cabozantinib, regorafenib, ramucirumab, brivanib, S-1, axitinib, and pembrolizumab significantly improved PFS. They recommended regorafenib and cabozantinib as the best second-line treatment options [ 35 ]. Differing from our study, that research did not evaluate the endpoints of TTP, ORR, and DCR, which introduces certain limitations to its results. In our study, regorafenib and cabozantinib are identified as the optimal second-line treatments, not only significantly improving OS and PFS but also showing advantages in DCR, TTP, and ORR, which is consistent with previous study results. The detailed comparison information between the different studies can be found in Table S2.

Strengths and limitations

Compared to previous studies, our research offers several significant advantages: First, the first-line treatment regimens are not limited to patients with sorafenib resistance or post-treatment progression, but also include other treatment options such as ICIs, other targeted therapies like lenvatinib, systemic chemotherapy or combinations of targeted and immune therapies. Second, all the studies we included are phase III RCTs, ensuring high-quality evidence. Third, the range of second-line treatment regimens considered is broad, not restricted to single-agent targeted therapies or immunotherapies. Fourth, we conducted a comprehensive evaluation of multiple outcome indicators, including OS, PFS, TTP, ORR, DCR, all-grade and grade 3–4 AEs, and the rate of treatment discontinuation due to AEs. Additionally, we updated the included literature to ensure the recency and comprehensiveness of our data. This demonstrates the thoroughness of our analysis. To the best of our knowledge, this is the most comprehensive systematic review and NMA comparing the efficacy and safety of all second-line treatments for HCC. This study includes the most extensive range of drugs and evaluates the broadest set of outcome indicators.

Despite the many important conclusions drawn from this study, several limitations should be noted. First, there are baseline differences among patients in the different studies, such as varying AFP levels and ECOG performance statuses, which may limit the generalizability of our conclusions. Second, although this study evaluated the efficacy and safety of second-line treatments using seven outcome indicators, not all indicators included all second-line treatments. For instance, studies on ADI-PEG20 only reported OS and PFS, without other efficacy-related outcome indicators. Third, we used the rate of treatment discontinuation due to AEs as one of the safety evaluation indicators. However, considering that the study population may have underlying cirrhosis, the degree of treatment discontinuation could be confounded by the severity of underlying liver disease, potentially introducing bias. Lastly, the quality of life for advanced HCC patients is also an important measure of drug efficacy, but due to a lack of relevant data, we did not evaluate the impact of second-line treatments on quality of life.

In summary, while current limitations present challenges, the future of liver disease management is promising. To address the baseline differences among patients, future research must prioritize the standardization of patient selection criteria and stratification methods. This will improve the generalizability of conclusions. Moreover, as whole-genome sequencing technology becomes more widespread and sophisticated, the assessment of treatment outcomes and prognosis for liver cancer patients is progressively shifting towards a more personalized and precise approach. We anticipate the integration of precision medicine approaches, leveraging genomic, proteomic, and metabolomic data to tailor treatments to individual patients. This advancement is expected to lead to substantial improvements in treatment efficacy, safety, and patient quality of life.

Despite these limitations, our study provides a comprehensive summary of RCTs for second-line treatments in advanced HCC. It demonstrates that different second-line treatments have their own advantages and disadvantages in terms of efficacy and safety. Considering both safety and efficacy, regorafenib and cabozantinib emerge as the optimal second-line treatment options for advanced HCC patients.

Data availability

No datasets were generated or analysed during the current study.

Availability of data and materials

All data generated or analysed during this study are included in this published article.

Abbreviations

• Hepatocellular carcinoma

Network Meta-analysis

Randomized Controlled Trials

Overall Survival

Progression-free Survival

Time to Disease Progression

Disease Control Rate

Objective Response Rate

Adverse events

Barcelona Clinic Liver Cancer,

Eastern Cooperative Oncology Group

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Acknowledgements

I would like to thank my supervisor, Dr. Shiping Hu, for his quidance througheach stage of the process.

Our research was supported by the National Natural Science Foundation of China (81973733), Shenzhen Municipal Commission of Science and Technology Innovation Meeting Projects (JCYJ20220530172812028), Technology Innovation Bureau of Longgang District, Shenzhen City Support Program (LGKCYLWS2022006).

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Fenping Lu and Kai Zhao are co-first authors.

Authors and Affiliations

Beijing University of Chinese Medicine, Beijing, China

Fenping Lu, Guangyan Xing, Bowen Liu & Xiaobin Li

Beijing University of Chinese Medicine Affiliated Shenzhen Hospital, Shenzhen, China

Fenping Lu, Guangyan Xing, Bowen Liu, Xiaobin Li, Yun Ran, Fenfang Wu & Shiping Hu

Shaanxi Shuangbo Hospital of Traditional Chinese Medicine for Liver and Kidney Diseases, Xi’an, China

Shaanxi Provincial Hospital of Traditional Chinese Medicine, Xi’an, China

Miaoqing Ye

Department of Pharmacy, Emergency General Hospital, Beijing, China

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Contributions

Fenping Lu,Kai Zhao (Co-frst author): Conducted literature searches and screened articles for inclusion. Performed data extraction and quality assessment of studies. Analyzed and interpreted the data. Drafted and revised the manuscript. Miaoqing Ye, Guangyan Xing: Conducted literature searches and screened articles for inclusion. Performed data extraction and quality assessment of studies. Analyzed and interpreted the data. Drafted and revised the manuscript. Bowen Liu, Xiaobin Li: Advised on study design and data analysis. Reviewed and provided feedback on manuscript drafts. Yun Ran, Fenfang Wu, Wei Chen: Contributed to the interpretation of the data. Reviewed and provided feedback on manuscript drafts. Shiping Hu(Corresponding author):Conceptualized the study and secured funding. Provided guidance on study design and data analysis. Facilitated communication among the authors. Ensured adherence to ethical standards and manuscript guidelines. Reviewed and provided feedback on manuscript drafts. Submitted the manuscript for publication. All authors read and approved the final manuscript.

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Lu, F., Zhao, K., Ye, M. et al. Efficacy and safety of second-line therapies for advanced hepatocellular carcinoma: a network meta-analysis of randomized controlled trials. BMC Cancer 24 , 1023 (2024). https://doi.org/10.1186/s12885-024-12780-y

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Received : 01 June 2024

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DOI : https://doi.org/10.1186/s12885-024-12780-y

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