Benefits to a Double-Blind Study

A case-control study is an observational study where researchers select a number of subjects with an outcome of interest (cases), and a number of subjects without the outcome of interest (controls). The prevalence of exposure to a risk factor is then compared between the two groups. If the cases have a much higher rate of exposure to the risk factor than the controls, it may mean that the outcome is related to the risk factor Example:
To evaluate if cell phones cause brain cancer, researchers select two groups of subjects Case group. 100 people with brain cancer Control group: 100 people without brain cancer Researchers then compare cell phone use between the two groups If cell phone use is much higher in the case group then there may be a link between brain cancer and cell phone use

Advantages
Much easier and cheaper to perform than a randomized controlled trial With modern medical databases, a large number of subjects can be evaluated with very little effort Outcomes with a low incidence can be evaluated. This is typically not feasible with a randomized controlled trial. Exposures that are not ethical in a randomized controlled trial can be evaluated. For example, no randomized controlled trial is going to randomize patients to smoking or known carcinogens.

Disadvantages
Does not prove causality Data for patient variables may be lacking or missing and therefore must be estimated Difficult or impossible to control for confounding Patients are not randomized so there is no way to control for unmeasured covariates and hidden bias

A cohort study is an observational study that is used to evaluate whether an exposure is associated with a particular outcome In a cohort study, two groups of subjects are formed based on exposure to a factor. One group has been exposed to a factor, and the other group has not been exposed to the factor. For other variables (ex. age, sex, race, etc.), the groups are matched as closely as possible Neither group has the outcome at the beginning of the study The two groups are followed for a length of time, and the incidence of the outcome is compared between the two groups A higher incidence in the exposed group may mean a link exists between the factor and the outcome Example:
Researchers want to evaluate if smoking causes bladder cancer They identify 2 cohorts of people: Exposed cohort: 100 smokers Control cohort: 100 nonsmokers They follow the two cohorts for a number of years and compare the incidence of bladder cancer between them

Advantages
Much easier and cheaper to perform than a randomized controlled trial With modern medical databases, a large number of subjects can be evaluated with very little effort Outcomes with a low incidence can be evaluated. This is typically not feasible with a randomized controlled trial. Exposures that are not ethical in a randomized controlled trial can be evaluated. For example, no randomized controlled trial is going to randomize patients to smoking or known carcinogens.

Disadvantages
Does not prove causality Data for patient variables may be lacking or missing and therefore must be estimated Difficult or impossible to control for confounding Patients are not randomized so there is no way to control for unmeasured covariates and hidden bias

A meta-analysis is a statistical study where the results from a number of related studies are pooled together and analyzed in order to draw conclusions from a broader set of data A meta-analysis may pool the results of cohort studies, case-control studies, randomized controlled trials, or a combination of the three. Cohort and Case-control studies may be combined in a meta-analysis, but it is not common (nor recommended) to combine randomized controlled trials with other types of studies

Advantages
Often times, different studies on the same condition will come to different conclusions. A meta-analysis is a way to combine the results of these studies so that an overall effect can be estimated. If a trial has a small number of subjects, it may not be powerful enough to find a statistically significant result. A meta-analysis allows small trials to be pooled together so that they have sufficient power to find a significant effect if one exists. The overall effect found in meta-analyses is often less than what is seen in individual trials. When done properly, the effect in the meta-analysis is more likely to represent the true effect in a large population of patients.

Disadvantages
Studies differ in length, design, intervention, population characteristics, and outcome measures. This can make it difficult to determine which studies to include. Combining studies that differ in design may lead to conclusions that are invalid Meta-analyses are subject to publication bias. Publication bias occurs when only studies that found a significant effect or a large effect were published. Meta-analyses are only as good as the studies they evaluate. If there are not enough good studies to perform a valid meta-analysis, the authors should be willing to concede this and abandon the meta-analysis. It can be argued that the results from a large, randomized controlled trial are more valid than the results of a meta-analysis on the same topic

A nested case-control study is a case-control study where the subjects for the study are sampled from a cohort of patients that has been observed for a period of time. The study is said to be "nested" within the cohort. Researchers form two groups from the cohort of patients. One group has the outcome of interest (cases), and one group has not developed the outcome (controls). Exposure to a risk factor can then be compared between the two groups. If the cases have a significantly greater exposure to the risk factor, then the risk factor may be related to the outcome. When selecting the control group in a nested case-control study, the researchers typically select 1 - 4 controls per case as opposed to comparing cases to the entire group of controls. Controls are selected that match the cases on a number of measured variables (ex. age, medical conditions, sex, etc). This helps to control for confounding. Example:
Researchers have observed a cohort of 100,000 women for 10 years At the start of the study, all women gave blood samples Over the course of the 10 years, 2000 women developed breast cancer The researchers are interested in finding out if there is a link between mercury exposure and breast cancer The researchers decide to test the blood samples for mercury levels and compare rates of breast cancer between women with high levels and those with normal levels Testing 100,000 blood samples for mercury levels would cost about $2 million dollars To save money, the researchers decide to do a nested case-control study where they select 2 controls for every case. Controls are selected that match the cases for a number of variables. This way they only have to test 6000 blood samples (2000 cases and 4000 controls).

Advantages
In most cases, the nested case-control study is much cheaper to perform than a full case-cohort study By selecting controls that match the cases on a number of covariates . there is some control for confounding and statistical efficiency should be improved

Disadvantages
Because the entire cohort is not used (for the controls), some precision is lost in the statistical measures, and the confidence intervals for the study outcomes will be wider Like regular case-control studies . nested case-control studies are observational studies and have all the same limitations

An observational study is a study where patients and outcomes are observed and no intervention is applied by the investigators. In observational studies, groups of subjects are formed according to specific exposures (cohort study ) or according to specific outcomes (case-control study ). This is in contrast to a randomized controlled trial where subjects are randomly assigned to a specific group and then followed. Observational studies may be prospective (groups are identified and then observed over time) or retrospective (groups are identified and outcomes are compared)

Advantages
Much easier and cheaper to perform than a randomized controlled trial With modern medical databases, a large number of subjects can be evaluated with very little effort Outcomes with a low incidence can be evaluated. This is typically not feasible with a randomized controlled trial. Exposures that are not ethical in a randomized controlled trial can be evaluated. For example, no randomized controlled trial is going to randomize patients to smoking or known carcinogens.

Disadvantages
The main disadvantage of observational studies is that there is no way to control for hidden bias and unmeasured covariates . In randomized controlled trials, the process of randomization helps to alleviate the effect of these issues.

RANDOMIZED CONTROLLED TRIAL (RCT)

A RCT is a prospective study where subjects are randomly assigned to either a treatment group or a control group In most studies, the two groups are matched as closely as possible by variables such as age, medical problems, lab values, blood pressures, etc. If the study is very large (ex. > 500 subjects), then these factors will often balance automatically through randomization. Randomization is very important because it is the only way to control for unmeasured covariates . Measured variables (ex. weight, age, medical history, etc.) can be adjusted for, but there may be variables that are not measured because the researchers are not aware that they can effect the study outcome. If the study is randomized and large enough, then unmeasured covariates should be distributed equally between the groups, and they will not bias the outcome. Randomization also prevents hidden bias. In observational studies . there is no way to prevent or control for hidden bias. In a RCT, the treatment group is given an intervention (drug or procedure) The control group is not given the intervention, or it is given a placebo or sham procedure The effect of the intervention is then measured over a predetermined time period by a predetermined set of outcomes RCTs are considered the gold standard for clinical trials, and if done correctly, their findings are much more consequential than those of other study designs (ex. cohort studies . case-control studies ) The best RCTs are placebo-controlled and double-blinded where possible

Advantages
Able to control for confounding from unmeasured covariates Hidden bias can be prevented Criteria and outcomes can be clearly defined and accurately measured Large RCTs will give the best measure of an intervention's effect in the intended population

Disadvantages
Expensive and time-consuming Can take many years to complete If an outcome has a low incidence, RCTs are typically not feasible because the study size would need to be very large, and it would make the trial very expensive RCT are not ethical in some situations. Example: Randomizing subjects to smoking or other interventions that are known to be harmful.

Certain countries, HMOs, and insurance companies maintain large databases of medical information on their citizens/patients/clients This information can be used to conduct observational studies Observational studies using medical databases as a source of information have become very popular because they allow investigators to examine a very large amount of information with very little effort, expense, and time Information from medical databases has a number of weaknesses that should be considered

Advantages
Cheap and easy to perform Able to evaluate a large amount of information with very little effort

Disadvantages
Diagnostic codes are often used as criteria. Use of these codes is not well-standardized. Pertinent patient information is often missing or not recorded and must be estimated Only can be used for observational studies

In an as-treated analysis, outcomes for subjects in a study are counted toward the treatment they actually receive. If a subject is randomized to one treatment group, but crosses over during the study and receives a competing treatment, then their outcome counts toward the competing treatment. This differs from an intention-to-treat analysis where a participant's outcome counts toward their original assigned group regardless of whether they crossover As-treated analyses are often performed in studies where there is a high amount of crossover between treatment groups On the surface, as-treated analyses seem to make sense, but in reality, they are susceptible to a large amount of bias Example:
A trial enrolls 200 people with sciatic nerve pain 100 people are randomized to physical therapy, and 100 people are randomized to back surgery The subjects are followed for one year. At the end of one year, differences in back pain and disability are compared. During the course of the year, 30 people assigned to physical therapy end up undergoing back surgery, and 10 people assigned to surgery never actually have surgery and instead receive physical therapy (crossovers) The researchers decide to do an as-treated analysis of their data so that the crossovers will be counted toward the therapy they actually received

Bias in as-treated analyses
In this example, all the patients who crossed-over are counted toward the treatment they actually received: 30 people from the physical therapy group are counted toward surgery, and 10 people from the surgery group are counted toward physical therapy This appears to be logical since the outcomes for crossovers will count toward the treatment they actually received. In reality, the analysis will likely be biased. People often enter trials because they hope to receive one of the treatments being offered. Trial protocols often allow for crossover at some point because this makes it easier to get people to participate. If a patient believes the only thing that will make his sciatic pain better is surgery (the perception that an invasive treatment is actually doing something where other treatments are not), and they are assigned to the physical therapy group, then that patient may be disappointed and is already biased toward not improving. The same patient may later crossover and receive surgery and only then get better because "something has been done." If this patient is counted toward the surgery group, then bias has been introduced. Another issue with as-treated analyses is that randomization is compromised. Randomization is one of the most important statistical methods that protects against bias and confounding (see randomization below)

In double-blind trials, neither the subject nor the researcher evaluating the subject knows which intervention the subject is receiving In single-blind trials, only the subject is blinded as to what intervention they are receiving Double-blinding helps prevent bias on the part of the subjects and the researchers When possible, randomized controlled trials should be double-blinded Double-blinding is not always possible. For example, when comparing a surgical intervention to a medical one.

Intention-to-treat is a method in randomized controlled trials where the outcomes for all participants who are randomized to a certain treatment or control group are counted toward that group regardless of whether they complete their assigned treatment protocol or not In an intention-to-treat analysis, outcomes for patients who stop treatment or drop out of treatment are still counted toward their original randomized group. Even outcomes from patients who crossover and receive a competing treatment are still counted toward the original assigned group. Intention-to-treat analysis is the gold standard for analysis, because other forms of analyses (see per-protocol analysis . on-treatment analysis . modified intention-to-treat analysis . and as-treated analysis ) can introduce bias into a study

Example:
A trial enrolls 200 people with sciatic nerve pain 100 people are randomized to physical therapy, and 100 people are randomized to back surgery The subjects are followed for one year. At the end of one year, differences in back pain and disability are compared. During the course of the year, 30 people assigned to physical therapy end up undergoing back surgery, and 10 people assigned to surgery never actually have surgery and instead receive physical therapy (crossovers)

Intention-to-treat
In an intention-to-treat analysis, outcomes for the 30 people who crossed-over from the physical therapy group and received surgery would still be counted toward the physical therapy group Outcomes for the 10 people who never underwent surgery will still be counted toward the surgery group

Advantages
Limits bias - In the above example, if an as-treated analysis was performed where all the patients who crossed-over were counted toward the group they ended up in, then bias would be introduced. People often enter trials because they hope to receive one of the treatments being offered. Trial protocols often allow for crossover at some point because this makes it easier to get people to participate. If a patient believes the only thing that will make his sciatic pain better is surgery (the perception that an invasive treatment is actually doing something where other treatments are not), and they are assigned to the physical therapy group, then that patient may be disappointed and is already biased toward not improving. The same patient may later crossover and receive surgery and only then get better. If this patient is counted toward the surgery group, then bias has been introduced.

Disadvantages
High crossover or dropout rates can bias a study towards the null (no effect) - If a study has a high crossover or dropout rate, then the study may be biased towards the null, or "no effect." In the above example, the 30 patients who crossed over to surgery are still counted toward physical therapy. If a true difference in outcomes exists between the two treatments, it will be harder to discern since positive surgery outcomes may count toward physical therapy. In the end, there is no perfect way to deal with crossovers and dropouts, but the gold standard for evaluating subjects in a trial is intention-to-treat.

Modified intention-to-treat is when investigators in a trial use an intention-to-treat analysis, but they modify who they include in this analysis Example:
A study wants to compare the effects of a new drug on postmenopausal vaginal dryness 100 women are randomized to the drug, and 100 women are randomized to placebo At the start of the study, all women have a vaginal smear performed After 6 months, changes in vaginal symptoms are measured The researchers present their significant findings in a "modified intention-to-treat" analysis where only women who had ≤ 5 superficial cells on their vaginal smear were included in the analysis

In the above example, the researchers decided to only include a subset of the randomized women in their analysis A modified intention-to-treat analysis should raise red flags because it may mean the researchers did not find a significant result with their intention-to-treat analysis, and they are now digging for a significant results by changing the study's criteria. This is bad form because it can introduce bias. A reviewer should also ask themselves if the modified criteria is clinically relevant. In the above example, most doctors are not going to do a vaginal smear before prescribing a menopause drug, so the fact that it may work in this subset of women is irrelevant. In some cases, a modified intention-to-treat analysis has little impact. Example: researchers do a modified intention-to-treat analysis that only includes randomized patients who received at least one dose of a study drug.

On-treatment analysis is when investigators only include data from patients while they are taking their assigned treatment. If patients stop their assigned treatment for a period, data from that time period is excluded. On-treatment analysis is similar to per-protocol analysis On the surface, on-treatment analyses makes sense - if someone stops treatment then their results should not count since the intervention can not help them if they do not take it In reality, on-treatment analysis introduces bias (See Examples below) Example #1:
A study is comparing a new drug to prevent migraines to an older drug that prevents migraines 100 people are randomly assigned the new drug, and 100 people are randomly assigned the old drug The patients are supposed to take the drugs for 6 months, and the number of migraines in that time period are recorded 30 people taking the new drug and 10 people taking the old drug stop taking it before the end of the trial The researchers decide to do a on-treatment analysis that excludes data from people while they stopped taking their drugs In this circumstance, the on-treatment analysis has introduced bias People stop study medications for a variety of reasons (e. g. side effects, lack of perceived efficacy, etc.). If a on-treatment analysis is performed, the study has been biased towards "responders" and it does not reflect the true efficacy of the drug in the intended population. This may also lead to spurious significant results.

Example #2:
A study is comparing aspirin to placebo for the prevention of deep vein thrombosis 1500 people are given aspirin and 1500 people are given placebo. The 2 groups are followed for 2 years and the rate of deep vein thrombosis is compared. 300 people in the aspirin group stopped taking their aspirin during the trial The researchers do a on-treatment analysis that excludes data from people while they stopped their aspirin. The analysis shows that when compared to placebo, patients who actually took their aspirin had better outcomes than the whole aspirin group (takers and non-takers). On the surface, this analysis seems legitimate. The outcome is objective, and for the most part, people tolerate aspirin well, so comparing people who actually took the drug to the controls makes sense. The problem is that past studies have shown that outcomes in the placebo group also differ between compliant and noncompliant patients. Patients who are compliant in taking their placebo are also more likely to have better outcomes than patients who do not (even for objective outcomes like heart attack). This phenomenon likely occurs because of differences in unmeasured confounders between compliant and noncompliant patients. Because of this phenomenon, the on-treatment analysis leads to erroneous results and is biased.

Overview
In a per-protocol analysis, only subjects who completed the protocol they were assigned to are included in the statistical analyses Patients who vary from the protocol (ex. stop medication), drop out of the study, or crossover to another therapy are not counted in the analyses Per-protocol analyses are similar to on-treatment analyses Per-protocol analyses introduce bias in many cases (see Example #2 and Example #3 below) Per-protocol analyses may be more meaningful in conditions that are difficult to treat and/or when there are few treatment options

Noninferiority trials
In noninferiority trials, per-protocol analyses should be reported with intention-to-treat analyses Noninferiority trials often compare new treatments to standard treatments (ex. new anticoagulant drug compared to warfarin for atrial fibrillation) During the trial, patients assigned to the new treatment may be allowed to crossover to the standard treatment for various reasons (e. g. side effects, new indication, etc.). In intention-to-treat analyses, crossovers can bias a study towards the null, or in the case of noninferiority trials, towards noninferiority. Per-protocol analyses should be reported with intention-to-treat analyses to help measure the sensitivity of the results to protocol violations


Example #1:
A study is comparing a new drug + standard therapy to standard therapy alone in a difficult to treat cancer The new drug has many side effects that make it intolerable for a number of patients. These patients stop taking the drug. The researchers decide to to do a per-protocol analysis to see if the new drug improved survival in patients who actually completed therapy In this case, the per-protocol analysis is meaningful because it will show whether people who can tolerate the therapy actually benefit from it

Example #2:
A study is comparing a new drug to prevent migraines to an older drug that prevents migraines 100 people are randomly assigned the new drug, and 100 people are randomly assigned the old drug The patients are supposed to take the drugs for 6 months, and the number of migraines in that time period are recorded 30 people taking the new drug and 10 people taking the old drug stop taking it before the end of the trial The researchers decide to do a per-protocol analysis that would exclude the people who stopped taking their drugs In this circumstance, the per-protocol analysis has introduced bias People stop study medications for a variety of reasons (e. g. side effects, lack of perceived efficacy, etc.). If a per-protocol analysis is performed, the study has been biased towards "responders" and it does not reflect the true efficacy of the drug in the intended population. This may also lead to spurious significant results.

Example #3:
A study is comparing aspirin to placebo for the prevention of deep vein thrombosis 1500 people are given aspirin and 1500 people are given placebo. The 2 groups are followed for 2 years and the rate of deep vein thrombosis is compared. 300 people in the aspirin group stopped taking their aspirin during the trial The researchers do a per-protocol analysis that excludes the people who stopped their aspirin. The analysis shows that when compared to placebo, patients who actually took their aspirin had better outcomes than the whole aspirin group (takers and non-takers). On the surface, this analysis seems legitimate. The outcome is objective, and for the most part, people tolerate aspirin well, so comparing people who actually took the drug to the controls makes sense. The problem is that past studies have shown that outcomes in the placebo group also differ between compliant and noncompliant patients. Patients who are compliant in taking their placebo are also more likely to have better outcomes than patients who do not (even for objective outcomes like heart attack). This phenomenon likely occurs because of differences in unmeasured confounders between compliant and noncompliant patients. Because of this phenomenon, the per-protocol analysis leads to erroneous results.

In a placebo-controlled trial, subjects who are not randomized to an active treatment (controls) are given a fake or sham treatment instead (Ex. an inert pill or a procedure that is faked) Placebo-control prevents subjects in a trial from knowing whether they are receiving the active treatment. This prevents bias that can arise from a subject's expectations that an intervention works. Placebo-control is very important in trials where outcomes are subjective (ex. pain, disability, frequency of events that are not biologically measurable) It should be applied when possible in trials with objective outcomes

Propensity score matching (PSM) is a statistical technique used in observational studies . It helps to control for selection bias. In PSM, subjects who received a treatment are matched with subjects who did not receive the treatment based on the probability of receiving the treatment. The probability of receiving the treatment is reflected in the propensity score. The propensity score is calculated by combining the probability of receiving treatment for a number of measured covariates . When subjects with the same propensity score are compared, selection bias is limited Procedure:
Determine the probability of receiving the treatment for each measured covariate in the study (ex. age, sex, medical conditions, lab values, etc) For each subject, combine the probabilities of receiving the treatment based on their individual covariates. Derive the propensity score from this combination (usually with logistic regression) Create groups of subjects with the same propensity score. Subjects with the same propensity score will typically match closely on a number of covariates. Compare treated subjects to untreated subjects within these groups. There are a number of ways of doing this. See Propensity score techniques below. Perform multivariate analysis on the propensity-matched sample

Propensity score techniques
Direct comparison
In direct comparisons, treated and untreated individuals with the same score are matched and compared. Matching can be one-to-one, one-to-as many that match, and so on. Groups can also be stratified by propensity score and then strata can be compared directly A major disadvantage of direct matching is that depending on the method used, all of the available data may not be utilized. In addition, if strata are compared, residual confounding may occur.

Propensity score as a covariate
The propensity score can be used as a covariate in a multivariate model In this case, the outcome is the dependent variable, and the independent variables are the exposure/treatment and the propensity score If the probability of receiving the treatment (propensity score) is strongly associated with the outcome, then covariate adjustment for the propensity score will decrease the strength of association between the treatment and the outcome

Propensity score weighting
Propensity score weighting is a method where each individual in the sample is weighted by the inverse of their propensity score Using this method, subjects who are more likely to receive the treatment carry less weight, and subjects who are less likely to receive the treatment receive the most weight With inverse weighting, covariates that are associated with receiving the treatment/exposure (higher propensity score) are neutralized while covariates that are weakly associated with receiving the treatment (low propensity score) gain value. This helps to neutralize selection bias, creating a sample where covariate distribution is independent of treatment selection. [5,6]



Advantages
PSM is helpful when a large number of covariates are measured because it creates a comparison that minimizes selection bias regardless of whether patients match exactly on all of the covariates PSM simulates randomization of treatment for measured covariates (not for unmeasured covariates)

Disadvantages
PSM cannot control for unmeasured covariates and hidden bias

TERMINOLOGY:
Measured variables - patient variables (ex. age, sex, medical problems) that are measured before a trial begins Unmeasured covariates - patient variables that are not measured, but may be related to (and have an influence on) the outcome being evaluated. There may be several reasons these variables are not measured. Researchers may not be aware that they can affect the outcome, or the variables may be expensive to obtain (ex. genetic profiles on every patient enrolled) Hidden bias - any form of bias that may influence the outcome of a trial (ex. researchers assigning healthier patients to the treatment group (a form of selection bias))

RANDOMIZATION
Randomization is a process in clinical trials where patients are randomly assigned to different groups (ex. treatment and placebo) Ideally, the person enrolling the patients in the trial should have no idea which group the patient will be assigned to Randomization is a critical component of controlled trials because it is the only way to control for unmeasured covariates. Randomization also prevents hidden bias. If the trial is large (> 500 subjects), then randomization will typically create groups that are equal for a number of measured variables (ex. age, sex, medical problems, etc) Unmeasured covariates can also affect the trial outcome. If the trial is large enough, randomization will automatically balance unmeasured covariates between groups so that they will not affect the outcome. Randomization prevents hidden bias from occurring Randomization is the main reason randomized controlled trials are the gold standard for clinical studies. Observational studies cannot randomize participants, therefore they are always subject to unmeasured covariates and hidden bias.

In single-blinded trials, only the patient is blinded as to what treatment they are receiving. The investigators or treating doctors are aware of the treatment given. Contrast with double-blinded trials where the investigator and subject are blinded to the treatment allocation Double-blinding is preferred when possible because it prevents investigator bias

When discussing absolute risk and relative risk, it helps to consider the two measures together Absolute risk is the overall incidence of an outcome in an entire group or population Relative risk is the ratio of the incidence of an outcome between two groups Relative risk only considers the proportion of the participants who have the outcome in question where absolute risk considers the entire population being studied. This can lead to some large difference between the two measures.

As one can see from the example above, the relative risk reduction and the absolute risk reduction can be quite different (46% vs 2.3%) It's important to understand the difference, because medical literature will often emphasize a large relative risk reduction when the absolute risk reduction may be quite small and insignificant. From the example above, the drug company for Livelong will likely say that they "reduce the risk of heart attack by 46%." While this may be true, someone taking Livelong will only reduce their overall risk of heart attack by 2.3%.

INCIDENCE
Incidence is the proportion of a group that develops a disease (or experiences an event) over a specified period of time


Example:
100 people without diabetes are followed for 5 years At the end of 5 years, 10 people have developed diabetes The incidence of diabetes over the 5 years is 10%



PREVALENCE
Prevalence is the proportion of a group that has the disease (or has experienced an event) at a single time point


Example:
100 people are selected randomly 10 of the people in the group have diabetes The prevalence of diabetes in the group is 10%

A likelihood ratio is a statistical ratio used to quantify the predictive value of a medical test (typically a screening test) The likelihood ratio is the factor by which the post-test odds of a condition being present (positive likelihood ratio) or absent (negative likelihood ratio) are increased or decreased based on the results of a test The likelihood ratio can be multiplied by the pre-test odds of the condition being present to determine the post-test odds Post-test odds of disease = Pre-test odds X Likelihood ratio Mathematically, the likelihood ratio is calculated using the sensitivity and specificity of the test:
Example:
Test A is a screening test for heart disease Paul is a 60 year-old patient who based on his family history, age, and medical conditions has a probability of 25% of having heart disease
Convert 25% probability to odds = 25/75 = 0.33

Test A has a negative likelihood ratio of 0.1 and a positive likelihood ratio of 1.9
Equivalent to a Sensitivity of 95% and a specificity of 50%

If Paul has a negative test A, then his post-test odds of heart disease are 0.1 X 0.33 = 0.033 If Paul has a positive test A, then his post-test odds of heart disease are 1.9 X 0.33 = 0.627 Converting back to probability:
negative test = 0.033/1.033 = 0.032 or 3.2% probability positive test = 0.627/1.627 = 0.385 or 38.5% probability

In Paul's case, a positive test increases his probability of disease from 25% to 38.5% - not very helpful A negative test decreased his probability of disease from 25% to 3.2% - more helpful This is true because the test had a high sensitivity (low false negatives) and low specificity (high false positives)

NET RECLASSIFICATION INDEX/IMPROVEMENT (NRI)

The Net Reclassification Improvement (NRI). (also called "Index") is a statistical measure used to evaluate whether adding a measure to a predictive model will improve the predictive accuracy of the model. An example would be adding Coronary Artery Calcium Scores (CACS) to the Framingham risk model to see if the addition of the CACS improves the Framingham's ability to predict a heart attack. The NRI takes into account both correct and incorrect reclassifications.

The NRI is calculated in the following manner: In a study, take the people who had an event or outcome (events) Calculate the number of events who were reclassified into a higher risk category when the new measure was included Subtract the number of events who were reclassified into a lower risk category when the new measure was added Divide this number by the total number of people who had an event Now take the number of people who did not have an event or outcome (nonevents) Calculate the number of nonevents who were reclassified into a lower risk category when the new measure was added Subtract the number of nonevents who were reclassified into a higher risk category when the new measure was added Divide this number by the total number of people who did not have an event Add the two proportions together and you have the NRI

The formula for the NRI is as follows:

Example
The Framingham risk model uses age, gender, total and HDL cholesterol, smoking status, and systolic blood pressure to predict a person's 10-year risk of heart attack Researchers want to know if adding Coronary Artery Calcium Scores (CACS) to the model improves the risk prediction of the original Framingham model A cohort of patients is formed and their Framingham 10-year risk is calculated using the original risk model The patients also have their CACS measured at baseline The patients are followed for 10 years and the incidence of heart attacks is measured Each patient's predicted risk of heart attack is calculated using the original Framingham model. The risk is also calculated using a model that incorporates the CACS. The NRI is then calculated by comparing the two models

Interpretation of the NRI
It's important to understand what the NRI actually means because it is commonly misinterpreted


In the example above, let's assume the addition of the CACS to the Framingham model had the following effect:
71 patients with a heart attack are reclassified as higher risk 24 patients with a heart attack are reclassified as lower risk 790 patients without a heart attack are reclassified as lower risk 657 patients without a heart attack are reclassified as higher risk Total number of patients who had a heart attack - 209 Total number of patients who did not have a heart attack - 5669

The calculation of the NRI is as follows: Some people mistakenly interpret this as the addition of CACS correctly reclassifies 25% of the population studied This is not correct. The addition of the CACS correctly reclassified 22.5% of the population who had an event (0.225 X 209 = 47) and 2.3% of the population that did not have an event (0.023 X 5669 = 130) The percent of the total population correctly reclassified is 177/5878 = .03 or 3% Whether or not 3% is clinically significant will depend on the cost and convenience of the additional measure
The number needed to treat (often abbreviated "NNT") is the number of patients who must be treated with an intervention in order for one patient to benefit If the intervention is a screening test, it is the number of people who would have to be screened in order for one person to benefit from screening The NNT can also be referred to as the "Number Needed to Harm" (NNH) when talking about a side effect or adverse event The NNT is calculated by taking the reciprocal of the absolute risk reduction The NNH is calculated by taking the reciprocal of the absolute increase in adverse event Example:
The recent NLST trial (detailed here ) found that yearly CT scan screening reduced the absolute risk of lung cancer death by 0.33% in heavy smokers The number needed to screen is = 1/0.0033 = 303 patients This means 303 patients would have to be screened in order to prevent 1 lung cancer death






OVERVIEW
When most people think of comparing two outcomes, they think in terms of relative risk Relative risk is a comparison that uses fractions. It is the most intuitive way to compare two outcomes.




Example:
Drug A has been shown to reduce the risk of heart attack by 20% Most people understand that people taking Drug A will have 20% fewer heart attacks than people not taking Drug A



ODDS
When discussing odds ratios, it helps to review what odds are Odds are ratios. Odds are not fractions. This can be confusing.


Odds = the number of times that an event will occur for the number of times that it will not occur

Example:
3:1 odds means the event is likely to occur 3 times for every one time it does not occur So for every 4 tries, there will be 3 events and 1 non-event. This equals a probability of 75% (3/4).

To convert between odds and probability:

ODDS RATIO

An odds ratio is a ratio of two odds. Relative risk (sometimes called hazard ratios) is a ratio of two fractions. Because of this distinction, the odds ratio and the relative risk ratio do not always approximate each other. This can be confusing because many people mistakenly interpret odds ratios as relative risk ratios. As the prevalence of an outcome increases above 10%, the odds ratio and the relative risk start to diverge. This occurs because odds above 1:1 (0.50 probability) can run to infinity where a fraction (of a whole) is always between 0 and 1. This can lead to wide discrepancies between the odds ratio and the relative risk.

Example:
Let's assume a group of diabetics are followed for a year and 80% of them suffer a heart attack A group of nondiabetics is followed for a year and 20% of them suffer a heart attack We want to compare the risk of heart attack between the two groups The relative risk of heart attack in the diabetic group compared to the nondiabetics is (0.8)/(0.2) = 4. Diabetics have 4 times the risk of heart attack when compared to nondiabetics. Most people understand this. The odds ratio of a heart attack when comparing the diabetics to nondiabetics is (4)/(0.25) = 16. This differs from the relative risk. It means diabetics have 16 times the odds of a heart attack than nondiabetics. This comparison is not as intuitive for most people and will often be misinterpreted as 16 times the risk of heart attack.

Rules for interpreting odds ratios:
When the incidence of the outcome of interest is < 10% in the study population, then the odds ratio and the relative risk can be considered equivalent When the incidence of the outcome of interest is > 10% in the study population, and the odds ratio is > 2.5 or < 0.5, then the odds ratio will tend to exaggerate the magnitude of the association. In some circumstances the odds ratio can be converted to a relative risk (see below).

ODDS RATIO IN MEDICAL STUDIES

Case-control studies
Odds ratios are always reported in case-control studies because risk is not measured in these studies. The case group has 100% probability of the disease and the control group has 0% probability. The odds of exposure to a risk factor is compared between the two groups, therefore the results are reported as an odds ratio.

Cohort studies
Cohort studies often utilize logistic regression to control for covariates . Logistic regression yields an odds ratio. In some cases, the odds ratio can be converted to a relative risk. See formula below. [2]

CONVERTING AN ODDS RATIO TO RELATIVE RISK

If a cohort study uses logistic regression and reports an odds ratio, it can be converted to relative risk if the incidence of the outcome in the unexposed (control) group is known

OUTCOME MEASURES (SIGNIFICANT CLINICAL OUTCOMES VS SURROGATE ENDPOINTS)

SIGNIFICANT CLINICAL OUTCOMES
A significant clinical outcome is an outcome that has a significant effect on a person's health, functioning, or well-being Examples of significant clinical outcomes include: death, heart attack, stroke, blindness, paralysis, cancer

SURROGATE ENDPOINTS
Surrogate endpoints are measures that have been shown to be related to a significant clinical outcome

Groups

Placebo are an English alternative rock band, formed in London in 1994 by singer-guitarist Brian Molko and guitarist-bassist Stefan Olsdal. The band were soon joined by drummer Robert Schultzberg, who was replaced in 1996 by Steve Hewitt. Hewitt left the band in 2007 and was replaced by Steve Forrest in 2008.

also known as placeo members:
Brian Molko (Guitar) since 1994 Robert Schultzberg (Drums) between 1994 and 1996 (2 years) Stefan Olsdal (Bass) since 1994 Steve Forrest (Drums) since 2008 Steve Hewitt (Drums) in 1994 Steve Hewitt (Drums) between 1996 and 1 October 2007 (11 years) Robert Schultzberg between 1994 and 1996 (2 years)

genres: Britpop. Glam rock. Rock music. Synthpop. Indie rock. Synth rock. Alternative rock. Post-punk. Post-punk revival. Emo. Glam punk. Gothic rock albums: "Come Home", "Placebo", "36 Degrees", "Teenage Angst", "Nancy Boy" (disc 1), "Bruise Pristine", "Pure Morning", "You Don’t Care About Us", "Without You I’m Nothing", "Burger Queen Français", "Taste in Men", "Slave to the Wage", "Black Market Music", "Special K", "Black-Eyed", "English Summer Rain", "The Bitter End", "Sleeping With Ghosts", "This Picture", "Special Needs", "Protège-moi", "Once More With Feeling: Singles 1996–2004", "Twenty Years", "Song to Say Goodbye", "Because I Want You", "Meds", "Infra-Red", "Every You Every Me", "Live @ Rock am Ring 2006", "Extended Play ’07", "Live At La Cigale", "Covers", "Exclusive Session", "Battle for the Sun", "For What It’s Worth", "The Never-Ending Why", "Ashtray Heart", "The Hut Recordings", "Bright Lights", "We Come in Pieces", "ITunes Live: London Festival '09", "B Sides 1996-2006", "Trigger Happy Hands", "Live at Angkor Wat", "Running Up That Hill", "Greatest Hits", "B3EP", "Loud Like Love" some of the nominations and awards:
1999
nominated to Brit Award for British Video - "Pure Morning"

2005
nominated to Kerrang! Award for Best British Band

2006
nominated to Kerrang! Award for Best Single - "Infra-Red" Kerrang! Classic Songwriter Award

2007
nominated to Echo Award for Best International Rock/Alternative Group - "Meds"

2009
nominated to Kerrang! Award for Best Single - "For What It’s Worth" nominated to Kerrang! Award for Best Video - "For What It's Worth" nominated to Kerrang! Award for Best Album - "Battle for the Sun" nominated to MTV Europe Music Award for Best Alternative MTV Europe Music Award for Best Alternative

2010
nominated to Echo Award for Best International Rock/Alternative Group - "Battle for the Sun"

2014
nominated to World Music Award for World’s Best Song - "Too Many Friends" nominated to World Music Award for World’s Best Album - "Loud Like Love" nominated to Echo Award for Best International Rock/Alternative Group - "Loud Like Love"



official website: www. placeboworld. co. uk

Placebo is a musical group.

members:
Marc Moulin between 1971 and 1976 (5 years) Philip Catherine Jean-Pierre Onraedt Yvan de Souter Garcia Morales Francis Goya Bruno Castellucci Nicolas Kletchkovsky Freddy Rottier Johnny Dover Richard Rousselet since 1971

albums: "1973", "Ball of Eyes", "Placebo"

PLACEBO LYRICS

"The Never-Ending Why"

The atom will implode

The fragile kingdom fold

The tremor becomes a quake

And there's a body in the lake

And as the two of us rebel

Damn you all to hell

I wonder if that's all there is

Time will help you through

But it doesn't have the time

To give you all the answers to the never-ending why

The sound of silence grows

References Edit

U. S. National Institutes of Health - "Declaration of Helsinki", Human Participant Protections Education for Research Teams Shamoo, Adil E. and Irving, Dianne N. "Accountability in Research." 1993 in press - Public Responsibility in Medicine and Research, Boston, Oct. 21 - 22, 1993 Brennan, TA. "Proposed Revisions to the Declaration of Helsinki — Will They Weaken the Ethical Principles Underlying Human Research?" N Engl J Med. 1999 Dec 9;341(24):1852-3. Merson MH. "Ethics of placebo-controlled trials of zidovudine to prevent the perinatal transmission of HIV in the Third World." N Engl J Med. 1997 Sep 18;337(12):853-6.

Implementation issues

Adherence

The Coronary Drug Project [7] was intended to study the safety and effectiveness of drugs for long-term treatment of coronary heart disease in men. Those in the placebo group who adhered to the placebo treatment (took the placebo regularly as instructed) showed nearly half the mortality rate as those who were not adherent. A similar study of women similarly found survival was nearly 2.5 times greater for those who adhered to their placebo. [8] This apparent placebo effect may have occurred because:

Adhering to the protocol had a psychological effect, i. e. genuine placebo effect. People who were already healthier were more able or more inclined to follow the protocol. Compliant people were more diligent and health-conscious in all aspects of their lives.

Placebo recognition

Appropriate use of a placebo in a clinical trial often requires or at least benefits from a double-blind study design, which means that neither the experimenters nor the subjects know which subjects are in the "test group" and which are in the "control group". This creates a problem in creating placebos that can be mistaken for active treatments. It therefore can be necessary to use a psychoactive placebo. a drug that produces physiological effects that encourage the belief in the control groups that they have received an active drug.

A psychoactive placebo was used in the Marsh Chapel Experiment. a double-blind study in which the experimental group received the psychedelic substance psilocybin while the control group received a large dose of niacin. a substance that produces noticeable physical effects intended to lead the control subjects to believe they had received the psychoactive drug. The term "psychoactive placebo" is rare in the literature; but, when it is used, it always denotes a placebo of this type. For example, "Neither the experienced investigator nor the naive [subject] is easily fooled on the matter of whether he has received a psychedelic substance or merely a psychoactive placebo such as amphetamine. " [9]

ARTICLE II.3 FORBIDS1

ARTICLE II.3 FORBIDS2

Placebo controls in clinical trials in which there is virtually no risk from the withholding of the ‘best proven therapy’

ARTICLE II.3 FORBIDS3

WMA: November 2001

"The WMA… hereby affirms its position that… a placebo

Franklin G. Miller

National Institutes of Health 1 Howard Brody, Michigan State University

Abstract: The leading ethical position on placebo-controlled clinical trials is that whenever proven effective treatment exists for a given condition, it is unethical to test a new treatment for that condition against placebo. Invoking the principle of clinical equipoise, opponents of placebo-controlled trials in the face of proven effective treatment argue that they (1) violate the therapeutic obligation of physicians to offer optimal medical care and (2) lack both scientific and clinical merit. We contend that both of these arguments are mistaken. Clinical equipoise provides erroneous ethical guidance in the case of placebo-controlled trials, because it ignores the ethically relevant distinction between clinical trials and treatment in the context of clinical medicine and the methodological limitations of active-controlled trials. Placebo controls are ethically justifiable when they are supported by sound methodological considerations and their use does not expose research participants to excessive risks of harm. Keywords: placebo-controlled clinical trials, therapeutic obligation, clinical equipoise, risk-benefit assessment, scientific and clinical merit, clinical trials versus treatment

Randomized controlled trials (RCTs) became the leading method of testing treatment efficacy in the 1940s. From the beginning, ethical concerns were voiced about clinical trials involving control groups not receiving proven effective or standard treatment. Debate over the use of placebo controls intensified following the publication in 1994 of a New England Journal of Medicine "Sounding Board" article by Rothman and Michels, "The Continued Unethical Use of Placebo Controls" (1994). The authors appealed to the Declaration of Helsinki in support of their claim that placebo-controlled trials are unethical whenever they are used to evaluate new treatments for conditions when proven effective treatments exist. They cited a range of recently published articles in the medical literature that violated the ethical guidance of the Declaration of Helsinki. Additionally, they pointed to the regulatory policy of the United States Food and Drug Administration as a major reason for the continued unethical use of placebo controls.

Recently the World Medical Association issued a "Note of Clarification" concerning the stance of the Declaration of Helsinki on the use of placebo controls (World Medical Association 2001). This statement marks a fundamental departure from the revision of October 2000 (World Medical Association 2000), which reiterated more clearly an absolute prohibition of placebo controls to test the efficacy of new treatments when proven effective treatments exist for a given condition. The "Note of Clarification" states that placebo-controlled trials may be ethically justifiable despite the availability of proven effective treatment in two circumstances:

(1) Where for compelling and scientifically sound methodological reasons its use is necessary to determine the efficacy or safety of a prophylactic, diagnostic or therapeutic method, or (2) Where a prophylactic, diagnostic or therapeutic method is being investigated for a minor condition and the patients who receive placebo will not be subject to any additional risk of serious or irreversible harm. (World Medical Association 2001)

This fundamental change in the Declaration of Helsinki, which has not been accompanied by an ethical rationale, makes it important to examine critically whether placebo-controlled trials can be ethically justified in conditions for which proven effective treatments exist.

The ethical reasoning underlying a prohibition of placebo controls in randomized clinical trials when proven effective treatments exist has been presented most clearly and persuasively by the late Benjamin Freedman and his colleagues (Freedman 1987; 1990; Freedman, Glass, and Weijer 1996a; 1996b). They have developed two arguments in support of this ethical stance. First, the use of placebo-controlled [End Page 3] trials in the face of proven effective treatments violates the physician's therapeutic obligation to offer optimal medical care to patients. Second, testing new treatments against placebo when proven effective treatments exist lacks scientific and clinical merit. Linking these two arguments is the principle of clinical equipoise, first formulated by Freedman, which has become a widely accepted axiom governing the ethics of randomized controlled trials. Freedman and his colleagues characterize the ethical and scientific force of clinical equipoise as follows: That principle can be put into normative or scien - tific language. As a normative matter, it defines ethical trial design as prohibiting any compromise of a patient's right to medical treatment by enrolling in a study. The same concern is often stated scientifi - cally when we assert that a study must start with an honest null hypothesis, genuine medical uncertainty concerning the relative merits of the various treatment arms included in the trial's design. These principles allow for testing new agents when sufficient information has accumulated to create a state of clinical equipoise vis-à-vis established methods of treatment. At the same time they foreclose the use of placebos in the face of established treatment, because enrolling in a trial would imply that a proportion of enrollees will receive medical attention currently considered inferior by the expert community. (Freedman, Glass, and Weijer 1996b, 253)

Although these two arguments against placebo-controlled trials have intuitive plausibility, we contend that they are both mistaken. We attempt to demonstrate that they fail to withstand critical scrutiny in light of the ethically fundamental distinction between clinical research and clinical care, methodological considerations pertaining to the scientific validity of clinical trials, appropriate ethical standards of risk-benefit assessment for clinical research, and sound public policy for drug development. In the process of this critique, we argue that the principle of clinical equipoise conflates the ethics of clinical research with the ethics of clinical medicine and provides erroneous ethical guidance on the use of placebo-controlled trials.

Argument from Therapeutic Obligation

It is claimed that the use of placebo controls in clinical trials when proven effective treatments exist violates the duty of physicians to offer optimal medical care. Because patients who enroll in RCTs are seeking treatment, they should not be randomized to treatment known to be inferior. When existing treatments have been proven effective in previous RCTs, it is unethical to test an experimental or novel treatment against placebo, which is known to be inferior to standard treatment. Instead, new, promising treatments should be tested against standard, proven effective treatment. What makes it ethical to conduct an RCT comparing a new treatment with a standard treatment, but not with a placebo, is that experts in the clinical community are uncertain or in a state of disagreement about whether the new treatment is as good as or better than standard therapy. This state of uncertainty in the clinical community is known as "clinical equipoise" (Freedman 1987). Use of placebo controls in the face of proven effective treatment violates clinical equipoise because it is already known that the placebo is inferior to standard treatment.

Underlying both clinical equipoise and the therapeutic obligation of physicians is the principle of therapeutic beneficence, central to medical ethics. Physicians should promote the medical best interests of patients by offering optimal medical care; and the risks of prescribed treatments are justified by the potential therapeutic benefits to patients. Placebo-controlled trials of new treatments in conditions for which proven effective treatments exist contravene the principle of therapeutic beneficence. Placebo controls in this situation are contrary to the medical best interests of patients. Patients randomized to placebo forgo proven effective treatment or treatment with a novel intervention considered to be as good as or better than standard treatment. Accordingly, they are exposed to risks associated with lack of treatment that are not justified by potential medical benefits.

Critique of Argument from Therapeutic Obligation

The argument from therapeutic obligation and the principle of clinical equipoise as applied to placebo-controlled trials confuse the ethics of clinical medicine with the ethics of clinical research. Physicians in clinical practice have a duty to promote the medical best interests of patients by offering optimal medical care. In RCTs, however, physician-investigators are not offering personalized medical therapy for individual patients. Rather, they seek to answer clinically relevant scientific questions by conducting experiments that test the safety and efficacy of treatments in groups of patients. The process of treatment in RCTs differs radically from routine clinical practice. Treatment [End Page 4] is selected randomly, not by an individualized assessment of what is best for a particular patient. Patient volunteers and physician-investigators often do not know who has have been assigned to the experimental treatment and who to the control treatment, which may be a placebo. Protocols governing RCTs frequently restrict flexibility in dosing and use of concomitant medications. These features of research design are implemented to promote scientific validity, not to promote therapeutic benefit.

Owing to these fundamental differences in purpose and process, the ethics of clinical trials is not identical to the ethics of clinical medicine. Specifically, the obligations of physician-investigators are not the same as the obligations of physicians in routine clinical practice. Investigators have a duty to avoid exploiting research participants, not a therapeutic duty to provide optimal medical care. Accordingly, enrolling patient volunteers in placebo-controlled trials that withhold proven effective treatment is not fundamentally unethical as long as patients are not being exploited. Patients may be seeking medical benefits by enrolling in clinical trials; however, they are not being exploited if

1. they are not being exposed to excessive risks for the sake of scientific investigation; and

2. they understand that they are volunteering to participate in an experiment rather than receiving personalized medical care directed at their best interests.

Given the distinction between clinical trials and medical therapy, as a rule it is undesirable or ethically hazardous for physician-investigators to enroll in their studies individuals with whom they have an ongoing doctor-patient relationship, either for primary or specialty care. Physicians may properly perform the dual roles of treating physician and investigator; the ethical problem arises when these dual roles are undertaken simultaneously with the same patients. Conflicts between patient welfare and scientific investigation, inherent in clinical research (Miller, Rosenstein, and DeRenzo 1998), are compounded and the potential for exploitation is increased when investigators have an ongoing physician-patient relationship with research participants. We do not, however, suggest that combining these dual roles simultaneously is always unethical. The duality of roles may be acceptable if clinical trials pose only slight risks to participants or if they offer the possibility of therapeutic benefit for patients who have exhausted all standard therapy other than supportive or palliative care.

The ethical irrelevance of the therapeutic obligation and the principle of clinical equipoise are concretely illustrated in the case of placebo - controlled trials that carry little or no risk from placebo assignment, despite withholding proven effective treatment. Consider a placebo-controlled trial of a new treatment for allergic rhinitis. There exist proven effective treatments for this condition. Nonetheless, it is difficult to see what could be morally wrong about a short-term trial comparing a novel treatment for allergic rhinitis with a placebo (Emanuel and Miller 2001). Trial participants randomized to placebo may be more likely to suffer from mild to moderate discomfort associated with untreated allergic rhinitis. But individuals with this condition often forgo treatment, and short periods without treatment pose no risks to health. Many would probably consider this example to be a valid exception to an absolute prohibition of placebo-controlled trials in the face of proven effective treatments. Notice, however, the significance of recognizing an exception in this case and in comparable clinical trials. If it is ethically justifiable to conduct a placebo-controlled trial of a new treatment for allergic rhinitis, then what counts ethically is not denial of treatment but lack of substantial risk to participants. Furthermore, if placebo-controlled trials can be ethical when they pose low risk to research participants, then it is an open question whether they are justifiable in conditions such as depression and anxiety disorders, migraine or tension headaches, stable angina, and asthma. In patients with these conditions, randomization to placebo poses more serious risks of discomfort or temporary functional disability from lack of standard treatment but low risk of irreversible harm, provided that clinical trials implement appropriate safeguards for screening eligible participants, monitoring their condition, and withdrawing them from the trial and initiating standard treatment (Emanuel and Miller, 2001).

Freedman and his colleagues have not acknowledged any exception to clinical equipoise: "Finally, attempting to justify a study by saying that it does not cause too much harm to too many people fails to take account of the physician's or investigator's responsibility to each individual patient or subject" (Freedman, Glass, and Weijer 1996b, 254). Physician-investigators do have an obligation to each research participant. However, that obligation [End Page 5] is not one of therapeutic beneficence. Rather, it is an obligation not to exploit participants for the sake of scientific investigation. Defenders of clinical equipoise might object that placebo controls in the face of proven effective treatment are wrong even if they do not pose any risks of serious or lasting harm. This, however, begs the question at issue. If there is no therapeutic obligation in the context of RCTs, then there is no wrong per se in using placebo controls that involve withholding proven effective treatment.

The implications of adopting clinical equipoise for the ethics of clinical research in general, especially research without any prospect of medical benefit, deserve attention. If physician-investigators are subject to a therapeutic obligation in the case of clinical trials, which makes RCTs ethical only when they conform to clinical equipoise, it is puzzling that physician-investigators can ethically perform any research procedures that pose risks but no compensating therapeutic benefits to patient volunteers; for example, studies of pathophysiology that administer biopsies or lumbar punctures, or imaging procedures that use ionizing radiation. In other words, why should therapeutic beneficence govern clinical trials but not the whole of clinical research?

Weijer offers an answer to this question by presenting an ethical framework for the evaluation of the risks and benefits of clinical research that draws on a fundamental distinction between therapeutic and nontherapeutic procedures (Weijer 2000). Procedures "administered with therapeutic intent" must pass the test of clinical equipoise. Procedures not administered with therapeutic intent are subject to an ethical requirement of minimizing risks and are justified by their potential to generate scientific knowledge. According to this framework, the principle of therapeutic beneficence applies to therapeutic procedures but not to nontherapeutic procedures.

We contend that this distinction is dubious. The most plausible candidates for therapeutic research procedures are experimental (or standard) treatments evaluated in clinical trials. However, as we noted above, the intent or purpose of administering treatments in clinical trials is not to provide personalized therapeutic benefit but to test hypotheses concerning safety and efficacy of treatments in groups of patients. Personalized attention characteristic of medical therapy is lacking in clinical trials that provide treatment according to a scientific protocol. This makes it misleading to characterize such treatment as therapeutic in intent.

Nevertheless, let us grant for the sake of argument that treatments evaluated in RCTs are therapeutic procedures. Application of Weijer's framework for ethical evaluation of the risks and benefits of clinical research leads to the conclusion that clinical equipoise is irrelevant to placebo-controlled trials. Weijer illustrates his ethical framework with four examples, including "Study A: Placebo-controlled trial of a drug for people with acutely symptomatic schizophrenia." After noting that "In study A, a novel antipsychotic is compared with placebo," he makes the surprising claim that "Both of these procedures are therapeutic interventions" (Weijer 2000, 354). No rationale is provided for describing a placebo control as a therapeutic procedure. Despite the possibility that placebo interventions may produce therapeutic benefit, placebo controls are properly classified only as nontherapeutic procedures employed to test the efficacy of novel treatments (Levine 1986, 204). The goal of a placebo-controlled trial is not to test the therapeutic efficacy of placebos. Placebo controls are sham treatments—that is, they are not treatments at all but control interventions designed to mimic a treatment subject to experimental evaluation. Accordingly, placebo controls under Weijer's framework should be assessed ethically not under the principle of clinical equipoise, but under the risk-benefit standards governing nontherapeutic procedures. With respect to the specific example of a placebo-controlled trial in schizophrenia, we think it would be difficult to justify the risks of symptom exacerbation from withholding antipsychotic treatment for those randomized to placebo.

Just as it is ethically justifiable to conduct nontherapeutic studies that pose some, but not excessive, risks of harm without the prospect of medical benefit, so it can be ethical to use placebo controls in scientifically valuable RCTs that involve withholding proven effective treatment, provided that the risks are not excessive and participants give informed consent. We conclude that the argument from therapeutic obligation against placebo - controlled trials fails. Placebo-controlled trials are not unethical just because they withhold proven effective treatment.

A Challenge and Response

The position that placebo-controlled trials may be ethically justifiable despite the existence of proven effective treatment, provided that risks to participants are not excessive, may be challenged on two grounds. What counts as excessive risk? And, who [End Page 6] decides? In the case of placebo-controlled trials, the answers to these questions about risk-benefit assessment are no different in principle than in the case of clinical research without any prospect of medical benefit for participants. Risks of placebo-controlled trials must be minimized, consistent with the possibility of a valid test of study hypotheses. In addition, risks that are not compensated by medical benefits to participants should not exceed a tolerable threshold, which may vary somewhat depending on the value of the anticipated scientific knowledge. Risks of concern include death, irreversible damage, temporary disability, and short-lived but severe discomfort. However, there is no reasonable way to formulate exactly the probability, severity, and duration of potential harm that would make the risks of placebo controls excessive. It calls for judgment. Such risk-benefit judgments are made by research sponsors, investigators, and, most important, by institutional review boards (IRBs) and research participants. If IRBs are properly empowered to make risk-benefit assessments for nontherapeutic research, they should also be responsible for determining when placebo-controlled trials are methodologically necessary or desirable and their risks tolerable, despite the existence of proven effective treatment. Finally, once proposed placebo-controlled trials have been reviewed and approved by IRBs, patients make their own judgments about whether they are prepared to accept the risks of trial participation.

The Argument from Scientific and Clinical Merit

It is also argued that placebo-controlled trials in the face of proven effective treatment lack scientific and clinical merit (Rothman and Michels 1994; Freedman, Glass, and Weijer 1996a; 1996b). The purpose of RCTs is to answer clinically relevant scientific questions about the safety and efficacy of treatments, with the ultimate aim of improving treatment. When proven effective treatments exist, there is no scientific or clinical value in testing a novel treatment against placebo. Instead, we want to know whether the new treatment is as good as or better than standard therapy, not whether it is better than "nothing" or no treatment.

This argument fails to come to grips with the methodological limitations of active-controlled trials, especially when they are designed to test the equivalence or "noninferiority" of an experimental and a standard treatment (Temple and Ellenberg 2000a; 2000b). There are powerful methodological considerations in favor of placebo-controlled trials both in the initial efficacy testing of experimental treatments and in the comparative evaluation of new and standard treatments. No new treatment should be introduced into clinical practice unless the expert community can be confident that it is effective. Superiority to placebo in a double-blind RCT is generally considered to be the most rigorous test of treatment efficacy. Accordingly, new treatments should be tested initially against placebo before being approved or validated, unless the use of placebo controls poses substantial risks of serious harm from withholding proven effective treatment.

In addition to their superior rigor, two-arm placebo-controlled trials generally require fewer research participants than active-controlled trials, making them more efficient. The reason for this is that the anticipated difference between the new treatment and placebo typically is greater than that between the new and standard treatments (Leon 2001). The efficiency of placebo-controlled trials is ethically relevant because they permit rigorous testing with less cost than active-controlled trials, and they expose fewer research participants to potentially toxic or ineffective experimental treatments (Leon 2000). How many initial placebo-controlled trials should be conducted, given the need to replicate scientific findings, and how many subjects should be included are matters of debatable judgment. From an ethical perspective, initial placebo-controlled trials of new treatments for conditions with already existing proven effective treatments should not enroll any more patient volunteers than is necessary to achieve a convincing demonstration of efficacy.

As the argument from scientific and clinical merit correctly asserts, once a new treatment has been shown to be better than placebo, it is important to evaluate its comparative efficacy by testing it against an existing standard treatment in an RCT. Nevertheless, there remain strong methodological reasons for including placebo controls in many trials comparing new and standard treatments in disorders with high rates of placebo response where standard treatments are only partially effective and not consistently found to be superior to placebos in clinical trials (Emanuel and Miller 2001). Under these conditions, if a two-arm active-controlled trial between the new and the standard treatment shows no statistically signifi-cant difference between them, two inferences are possible. Either both the new and the standard treatments were effective in the study sample; or neither the new treatment nor the standard treatment were effective (Temple and Ellenberg 2000a; [End Page 7] 2001b). Without a placebo control to validate the efficacy of the two treatments being compared, it may be difficult, if not impossible, to determine which inference is correct. Such active-controlled trials lack "internal validity." It follows that there are sound methodological reasons for including placebo controls in three-arm trials comparing new and standard treatments in conditions with high rates of placebo response where standard treatments are only partially effective, such as depression and anxiety disorders.

It might be objected that this appeal to methodological considerations in favor of placebo-controlled trials gives science priority over ethics (Rothman 2000). This objection rests on a false dichotomy. Scientific validity is an essential ethical requirement of clinical research (Emanuel, Wendler, and Grady 2000). No person should be subjected to risks of research participation in studies that lack scientific validity. It follows that sound methodological considerations in favor of placebo-controlled trials and against active-controlled trials are ethically relevant.

The argument from scientific and clinical merit also adopts the false premise that placebo-controlled trials test whether new treatments are better than nothing or no treatment. Despite the recently published meta-analysis of clinical trials with placebo and "no treatment" arms (Hrobjartsson and Gotzsche 2001), which cast doubt on the power and pervasiveness of the placebo effect, the jury remains out on whether the use of placebo controls is associated with therapeutic benefit. But even if placebo interventions in themselves are entirely lacking in therapeutic benefit, placebo controls are typically combined with interventions that have therapeutic potential. These include clinical attention from investigators and members of the research team, the therapeutic milieu of research hospitals, especially in the case of inpatient clinical trials, and ancillary treatments or rescue medications that are often provided to research participants randomized to placebo. Though participants randomized to placebo may receive treatment that is less than optimal, this is not the same as no treatment.

Conclusion

We conclude that both the arguments from therapeutic obligation, invoking clinical equipoise, and from scientific and clinical merit fail to establish that placebo-controlled trials are unethical or pointless whenever they evaluate treatments of conditions for which proven effective treatments exist. It does not follow that placebo-controlled trials are ethically innocuous. Placebo-controlled trials raise ethical concerns insofar as they have the potential to exploit research participants by exposing them to excessive risks from placebo assignment or by enrolling them without adequate informed consent. Additionally, they should not be conducted unless they have scientific merit. Reasonable ethical criteria for the justification of placebo-controlled trials have been presented elsewhere (Emanuel and Miller 2001; Miller 2000).

If our critique is sound, it has important implications for the ethics of clinical research. Appeal to the principle of clinical equipoise should be abandoned; or the scope of the principle should be limited so that it does not apply to placebo-controlled trials. Placebo controls should be evaluated according to the same ethical standards that apply to research procedures that pose risks without compensating medical benefits (Emanuel, Wendler, and Grady 2000).

Paul B. Miller, M. Phil. is a J. D./Ph. D. candidate in Law and Philosophy at the University of Toronto and a Junior Fellow of Massey College in Toronto. Mr. Miller has also studied history and philosophy of science and medicine at the University of Cambridge, Cambridge University in England where his dissertation focused on philosophical problems in the moral evaluation of research-related risks.

Advantages for participants

Clinical trials can be a life-line for patients who have exhausted the accepted treatment options because they offer new and promising approaches to treatment. The trial will most likely involve a medicine which is currently unavailable to the public, and it may be a more effective treatment with fewer side effects. While you participate in the study, your condition will be continually monitored and you’ll probably receive a greater level of care as a result.

Oral (Provocation) Challenges

An allergy diagnosis is made by a very careful history. skin prick tests, blood tests (Immuno-CAP RAST), Patch tests, Atopy Patch test & Oral Challenges. A Double-Blind Placebo-Controlled (DBPC) Oral food Challenge is considered the “gold standard” in the diagnosis of food allergies and some drug allergies.

The importance of taking a careful (thorough) history cannot be stressed enough, because not only can a good history give the diagnosis on its own, but it guides the Allergist towards stream-lined allergy testing. Random (battery) testing is financially wasteful and also time consuming and potentially misleading. The allergy tests should only be used to confirm a diagnosis that has been made based on the history.

The aim of oral food challenge is to study the consequences of food ingestion in an objective way. It is well known that the perceived prevalence of food allergies is much higher than the true prevalence, and this is due to the subjective symptoms that are often associated with food ingestion. This is due to a conditioned (Pavlovian) Response.

Clinical uses of oral challenges

To confirm a diagnosis of food allergy based on history and equivocal skin prick tests & / or Immuno-CAP RAST-type tests. The new Immuno-CAP tests are so sensitive & specific for diagnosing food allergies to milk, egg, peanut, fish, and wheat that oral challenges to these foods are very rarely done to diagnose allergy. To diagnose Food Intolerance, where skin tests & blood tests are expected to be negative (not useful). To see if a child has grown out of a food allergy, especially when the Immuno-CAP tests are equivocal. To re-assure patients who, would otherwise be unconvinced that their symptoms are not attributable to the foods that they have developed a conditioned response to. To confirm drug allergies.

Principles of Oral Challenge

The food challenge should replicate normal food consumption in terms of amount and state of the food. The period of observation after the ingestion should match the time period between ingestion & onset of symptoms based on the history.

If co-factors like exercise or ingestion of drugs like NSAIDs are required for the reaction, this has to be replicated in the challenge. For example in patients with food-related exercise-induced anaphylaxis, the ingestion of the suspected food has to be followed by exercise.

Types of Oral Challenges

Open Challenges – are the simplest oral challenges. The parents, doctor, and the patient know what food is being given. The freshly prepared food is given and the patient is observed for the required time based on the history. The main drawback to an open challenge is the risk of bias influencing the parents’, patient’s or doctor’s observations. If the parent’s belief in food allergy is expected to be disproportionately high, an open challenge should not be done. Single-blind challenges – In this case the observer (doctor or nurse) but not the patient or family know the test material. The drawback to this method is bias influencing the observer. Double-blind Placebo challenges – In this case either the challenge substance or an indistinguishable inactive (placebo) substance is administered. Neither the child, the parents or the observer know the identity of the administered material.

Challenge Procedure

A detailed history is essential to determine:
Which food/s are suspected. What symptoms are produced. How long after ingestion do the symptoms occur. What is the smallest quantity of food which will produce symptoms. The frequency of the reactions. How reproducible is the reaction, i. e. does the reaction always occur when the food is ingested. Whether the reaction only occurs in the presence of some additional factor, for example, does the reaction only occur if ingestion of the food is followed by exercise?

Elimination diet prior to the challenge
Suspected foods need to be avoided for approximately 2 weeks prior to the challenge, because regular consumption of the food could obscure a reaction to a single dose. It is well known that with food intolerance, regular intake of the foods like salicylates will lead to a state of tolerance to the food. The elimination diet also confirms the relevance of the eliminated foods being a trigger for the symptoms.

Preparation of foods for the challenge
Dehydrated or dried powdered foods is administered in opaque gelatin capsules or The food is disguised in a carrier food such as apple or vegetable puree or lentil soup. This method is more commonly used than the capsule method.

Placebos
If capsules are used, dextrose or lactose powder is the simplest placebo. The vehicles described above, without the addition of anything else can be used as the placebo.

Avoidance of medications
Drugs which should be avoided before the challenge include:
Antihistamines (for about 72 hrs) Cromoglycate (for 12 hrs)

If the foods cause reaction despite the medication, then the medication does not have top be avoided. Also, it is important to note that withdrawing the medication prior to the challenge may precipitate symptoms, which will interfere with the interpretation of the challenge symptoms.

Food Administration
This should start with a small quantity, less than that estimated (from the history) to cause symptoms. The dose is then doubled at 45 – 60 minutes intervals. The longer interval for reactions occurring later after the food ingestion (based on the history). The doubling of the dose is continued until the patient has obvious symptoms, or until about 10g of dried or 100g of untreated food have been given. In some cases of food intolerance (with delayed reactions) larger quantities of foods may be required.

Risk of Anaphylaxis during oral challenges

With a history of previous anaphylaxis related to the food being tested. Foods like peanuts, nuts, milk, egg, and fish carry a greater risk of anaphylactic shock than others. Patients with atopic eczema are at increased risk for anaphylaxis after strictly eliminating foods that they are allergic to, even though they never had anaphylaxis to that food previously.

Because of the risk of anaphylaxis oral challenges should be done in an environment that is set up to offer full resuscitation.

Pitfalls of Double-blind Placebo-Controlled (DBPC) oral food challenges

DBPC food challenges are considered the “gold standard” for diagnosis of adverse reactions to foods, but do they mimic real-life exposure?

To stop a DBPC food challenge & declare it positive or negative symptoms should be objective and /or repetitive.

Causes of false negative DBPC oral food challenge include :

Inadvertent drug use during the challenge. a short-term specific oral tolerance induction (SOTI) may be induced as increasing amounts of the offended food are administered during a titrated oral food challenge.

Causes of false positive DBPC food challenge include:

Difficulty in maintaining a strict diet throughout the oral challenge procedure. The elimination diet implemented before the challenge might be responsible for the “new” symptoms seen during the trial.

Cytisine for smoking cessation: as good as nicotine replacement &#8212; and cheap

Jan 10 2015

The smoking cessation drug varenicline (Chantix) works by weakly activating and also blocking nicotine receptors in the brain, simultaneously. This neat trick has the dual effects of reducing tobacco cravings while also blunting the "high" from smoking.

That combination has made Chantix the most successful smoking-cessation therapy on the market, but it costs about $500 for 12 weeks. Chantix sticker shock puts off many smokers who want to quit (even though most are already spending $150/month on cigarettes), if they weren't already scared off by varenicline's black box warning about psychiatric effects.

Like many prescription drugs, varenicline was inspired by a template already existing in nature: cytisine, an alkaloid in the seeds of the golden rain tree, native to central and southern Europe. Like varenicline, cytisine is a partial agonist of nicotinic acetylcholine receptors in the brain. Cytisine has been used as a smoking-cessation aid in the formerly communist states of Eastern Europe for decades, where it costs less than $30 for a 25-day course.

Golden rain tree, Laburnum anagyroides (courtesy: Wikipedia)

Multiple randomized trials and systematic reviews have shown that cytisine significantly improves the chances of quitting smoking compared to placebo. A new randomized trial in the New England Journal of Medicine is the first to test cytisine against nicotine replacement therapy.

1,310 smokers in New Zealand who had called the national quit hotline were randomized to receive either cytisine for 25 days or nicotine replacement therapy for 8 weeks. The therapies were provided free or at very low cost.

The phase III trial was funded by Extab. a company licensed to promote and sell cytisine (brand name Tabex) globally outside Central and Eastern Europe. Extab also funded a previous phase III trial. published in 2011, showing cytisine's superiority over placebo.

After a month, 40% of cytisine-takers reported continuous abstinence, compared to 31% of those getting nicotine replacement. The benefits held at 6 months, when 22% of those taking cytisine reported smoking abstinence compared to 15% of those using nicotine replacement.

Varenicline worked better than nicotine patches in one randomized trial, and meta-analyses suggest Chantix is better than nicotine replacement overall for smoking cessation. Cytisine's numerical advantage over nicotine replacement did not reach statistical significance in this trial.

Does cytisine have weird effects on the brain, like the well-known vivid dreams of Chantix? It may be too soon to say: about 5% of patients taking cytisine reported "sleep disorders" (due to dreams?) or nausea; strange dreams and nausea are among the most common reported side effects of varenicline. Extab's website interprets the trial results as a "strong safety and side-effect profile with no neuropsychiatric issues" from cytisine.

With this second phase III trial, Extab's goal of bringing cytisine profitably to the masses appears closer to realization. The European Medicines Agency is reviewing safety data from 8 million Central and Eastern European patients treated with cytisine. There is relatively little toxicity data available on cytisine. but it is known to cause respiratory suppression at high doses. Toxicologists have pointed out it is probably hard for humans to overdose on cytisine successfully. since large ingestions should produce severe vomiting.

The FDA turned down a 2006 request by supplement manufacturers to market cytisine as a supplement in the U. S. citing absence of safety data.

Extab hopes additional well-conducted clinical trials will overcome those concerns and establish cytisine's place as a safe and effective smoking cessation aid. Rick Stewart, Extab's CEO told Reuters recently. “Extab expects to commence additional Phase 3 clinical trials in 2015 with a goal of filing a New Drug Application with the U. S. Food and Drug Administration and a Marketing Authorization Application with the European Medicines Agency in late 2016.”

With its low cost and apparent effectiveness, cytisine seems to have great promise as a smoking cessation tool. But don't expect to see it for 2 years or longer in the E. U. or the U. S. The adventuresome smoker willing to accept the risk of safety, counterfeit medication, and violation of any applicable laws can buy cytisine online. where it is being sold eagerly as Tabex (or at least in boxes that say so) by Internet entrepreneurs.

Natalie Walker et al. Cytisine versus Nicotine for Smoking Cessation. N Engl J Med 2014; 371:2353-2362.

PulmCCM is an independent publication not affiliated with or endorsed by any other organization, society or journal referenced on the website. (Terms of Use | Privacy Policy )

Placebo-controlled, Double Blind Trial of Medicinal Cannabis in Painful HIV Neuropathy

INVESTIGATOR: Ronald Ellis, M. D. Ph. D.

STUDY LOCATION: University of California, San Diego

PROJECT TITLE: Placebo-controlled, Double Blind Trial of Medicinal Cannabis in Painful HIV Neuropathy

PROJECT TYPE: Clinical Study

Of 127 volunteers screened, 34 eligible subjects enarolled and 28 completed both cannabis and placebo treatments. Among completers, pain relief was greater with cannabis than placebo (median difference in DDS pain intensity change, 3.3 points, effect size = 0.60; p = 0.016). The proportions of subjects achieving at least 30% pain relief with cannabis versus placebo were 0.46 [95% CI 0.28, 0.65] and 0.18 [0.03, 0.32]. Mood and daily functioning improved to a similar extent during both treatment periods. Although most side effects were mild and self-limited, two subjects experienced treatment-limiting toxicities.

Smoked cannabis was generally well-tolerated and effective when added to concomitant analgesic therapy in patients with medically refractory pain due to HIV DSPN.

The full results of this study were published in the journal Neuropsychopharmacology.

Neuropathic pain continues to be a major clinical problem in HIV infection. The predominant cause is an axonal polyneuropathy, termed HIV-associated distal, sensory-predominant polyneuropathy (DSPN) that is variably associated with HIV itself or with the use of certain nucleoside analogue HIV reverse transcriptase inhibitors used in antiretroviral treatment regimens. Available treatments, including opioids and adjunctive pain-modulating agents, often are ineffective for pain control, resulting in disability and diminished quality of life for individuals with HIV infection. The proposed study will be a double-blind, placebo-controlled trial of medicinal cannabis for the short-term adjunctive treatment of neuropathic pain in HIV-associated DSPN. Case ascertainment will be by history, physical examination, nerve conduction studies and quantitative sensory testing. Thirty subjects will be enrolled in a double-blind, cross-over trial design. Because a safe and effective dosing range for cannabis for neuropathic pain has not been previously established, and because we anticipate that the frequency and magnitude of both beneficial antinociceptive and adverse drug effects with cannabis will differ substantially across individuals, a structured dose escalation-titration protocol will be used to find an individualized, effective, safe and well-tolerated and dose for each subject. The total study duration will be 3 years. The principal outcome measures will be changes in self-reported pain, disability in activities of daily living and indices of quality of life.