Three things you need for a power calculation (created 2001-11-08, revised 2011-04-26).
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Dear Professor Mean, I want to do research. Is forty subjects enough, or do I need more? -- Eager Edward
That reminds me of a cute joke. How many research subjects does it take to screw in a light bulb? At least 300 if you want the bulb to have adequate power.
Sorry, I was digressing. Is forty subjects an adequate sample size? That depends on a lot of factors. The basic idea, though, is to select a sample size which ensures that your study has adequate power. Power is the probability that your research study will successfully detect a difference, assuming that the treatment or exposure you are examining actually can cause an important difference. If you don't care whether your experiment is successful or not, then you can use just about any sample size.
Power is to a research design like sensitivity is to a diagnostic test. A diagnostic test with good sensitivity is normally able to detect a disease when the disease is present. A research study with good power is normally able to detect a change when your treatment is indeed effective.
The actual calculation of power requires three pieces of information:
- your research hypothesis,
- the variability of your outcome measure, and
- your estimate of the clinically relevant difference.
Calculating power is sometimes difficult and it may require you to go to the time and expense of running a pilot study. But you should NEVER start a research project without knowing what your power is. That would be like using a diagnostic test with unknown sensitivity.
A research hypothesis will provide specific information that will determine what type of analysis is needed. A common structure for a research hypothesis is specification of the subject group you are testing, the treatment or exposure that this group will receive, the outcome measure, and the comparison or control group.
Some exploratory studies may not have a research hypothesis, of course, and for those studies you determine an appropriate sample size in a different way (for example, by insuring that the estimates from this exploratory study have adequate precision).
Variability of your outcome measure
You also need to have an estimate of the variability of your outcome measure. I'm assuming here that your outcome measure is continuous variable like birth weight or cholesterol level. If you are using a categorical outcome measure like mortality or cancer remission, then you need some estimate of the rate of mortality or remission in your control group.
Your literature review (you did do a literature review before you started this research, I hope), will usually provide you with an estimate of variability. Select a study that is reasonably similar to what you plan to do, and find out what that study reported for the standard deviation for your outcome measure.
Although I prefer a standard deviation, other estimates of variability are also acceptable. If the paper reports a variance, a standard error, a confidence interval, or a coefficient of variation, then there are simple formulas for converting these into standard deviations. If the study priveds a range, then you can divide the range by four to get a good approximation for the standard deviation.
Many of the people I see have a difficult time providing any estimate of variability. This area hasn't been studied before, so no one knows what the variability will be. But don't give up too easily.
First keep in mind that you only need a crude estimate of variability. Power calculations are capable of determining if you are "in the right ball park." They are good at specifying your sample size down to an order of magnitude perhaps but not much more than that. In other words, might tell you whether you need hundreds of subjects dozens of subjects instead of hundreds of subjects, or possibly if you need thousands of subjects.
Second, although most research is innovative and therefore unique, this innovation is often in the treatment and not in the outcome measure. So look for studies that used the same outcome measure, even if the treatment is quite different than yours.
Third, try to characterize variability in your control group and we can try to extrapolate what the variability will be in the treatment group. A retrospective chart review, for example, will provide a rough estimate of variability of your outcome measure under the current standard of care.
Third, you may have to use a clearly flawed estimate, but a flawed estimate of variability may still be better than no estimate at all. An estimate of variability in adults, for example, may not be an ideal estimate for a pediatric study, but at least it tells you if your study will have adequate power assuming that the variation in a pediatric population is comparable to variation in an adult population. That's still better than having no idea whether your study has adequate power.
If you've tried and you still can't come up with an estimate of variability, then don't despair. A pilot study can provide you with an estimate of variability when all else fails. Usually 20 to 30 subjects produce a reasonably stable estimate of variability. A pilot study is also helpful for finding out how quickly you can recruit subjects. Furthermore, a pilot study will also identify any weaknesses in the logistics of your research. Finally, if the protocol remains substantially unchanged after the pilot study, you can usually include those pilot subjects in the final analysis.
Clinically relevant difference
Wow, that was exhausting! You're not done, though, until you can tell me what a clinically relevant difference would be for your outcome measure. This is a difference that is large enough to be considered important by a practicing clinician.
For just about every type of study, some differences are so small as to be clinically meaningless. From a theoretical viewpoint, perhaps, changes of any size might be interesting. But theory and practice are very different. If a six month diet program produces an average weight loss of three pounds, a fever medicine reduces average temperature by half a degree Fahrenheit, or a smoking cessation program helps an additional two percent to quit, who cares what the theoretical implicaitons might be.
It's not easy but this is something that you have to do for yourself. The clinically relevant difference is determined by medical experts and not by statisticians. Hey, I'm still trying to understand the difference between good and bad cholesterol; I wouldn't even be able to start thinking about how much of a change in cholesterol is considered clinically relevant. You might start by asking yourself "How much of an improvement would I have to see before I would adopt a new treatment?" Also, try talking with some of your colleagues. And look at the size of improvements for other successful treatments.
Still, there are some general guidelines that might help. Try looking at the resolution of your measuring device, thinking in terms of relative changes, or specifying changes with respect to your standard deviation.
Average changes that are smaller than the resolution of your measuring instrument are probably not clinically relevant. For example, Apgar scores can take on any whole number between 0 and 10. Gestational age can only be measured accurately to within a week In these contexts, it is clear that average changes should probably be greater than one unit in order to achieve relevance.
Still this is not a perfect rule. We can measure weights to within a gram, but changes in birth weight would have to be in the hundreds of grams or more to be meaningful. And while no family can have a fractional number of children, decreasing the average family size by 0.2 children can have a profound effect on society.
It also may help to think in terms of relative changes. If you can change something by 25 percent or 50 percent, that is considered relevant in most contexts. It becomes harder to argue clinical relevance for changes of less than 10 percent. Again, this is not a perfect rule.
Finally, you might find it easier to specify changes with respect to your standard deviation. This type of change is called an effect size. A common classification is that 0.2 standard deviations is considered a small effect size, 0.5 standard deviations is considered a medium effect size, and 0.8 standard deviations is considered a large effect size.
An effect size of 0.2 is small enough that there is no obvious visible separation between the two groups. The difference in average heights between 15 and 16 year old girls is 0.2 standard deviations. An effect size of 0.8 is clearly visible. The difference in average heights between 14 and 18 year old girls is 0.8 standard deviations.
It may be unrealistic to look for changes much smaller than 0.2 standard deviations because the sample sizes become prohibitively large. It may also be unrealistc to expect to see changes much larger than 0.8 standard deviations since this size change does not seem to occur too often in the published literature.
Like the other two rules, this rule is also not perfect. In some animal experiments, for example, the similarity in the gene pool can often reduce variation to such an extent that changes of more than a full standard deviation are quite realistic. If you are trying to specify a clinically relevant difference, there is no substitute for a good understanding of the context of your research.
But I can't do it.
A lot of people tell me that they can't do this. They can't provide an estimate of variability or they can't determine what a clinically relevant difference is, even after I explain all of the above suggestions.
But you have to do it.
The CONSORT Guidelines require you to have an a priori justification of sample size for publication. If you don't do this now, you won't be able to publish the data in any journal that uses these guidelines. What's the point of doing the research if you can't publish it?
If your research requires an ethical review (e.g., through an IRB), they will require the same a priori justification. If the research involves animals, the appropriate animal care and use committee will require this justification.
The bottom line is that if you know so little about this avenue of research that you can't even come up with a preliminary estimate of the variability of your outcome variable, then you shouldn't be doing the research. You need instead to:
- do a more thorough literature review,
- collect some pilot data, or
- switch to an outcome measure whose variability is known to some extent.
But do something, because your ability to perform the research and to publish your research depends on your justification of the sample size.
In a study of two different skin barriers for burn patients, we are interested in three outcome measures: pain, healing time, and cost. We will randomly assign half of the patients to one skin barrier and half to the other.
For pediatric patients we usually measure pain with the Oucher, a five point scale that has been validated for children. A review of previous studies using the Oucher have shown that it has a standard deviation of about 1.5 units. We would be interested in seeing how large a sample size is needed to show a change of 1 unit, the smallest individual change attainable on the Oucher. We want to have a power of .80, or equivalently, the probability of a Type II error of .20.
The formulas for sample size vary from problem to problem. The sample size needed for a comparison of two independent groups is
We use the letter "z" to represent a standard normal distribution. Alpha represents the probability of a Type I error (usually .05). Beta represents the probability of a Type II error (we usually want this to somewhere between .05 and .20). Sigma represents the standard deviation, and this formula allows for the possibility of different standard deviations in group 1 and group 2. Don't forget that the formula requires you to square these standard deviations. Finally, D is the clinically relevant difference. In our example,
We round up. So in order to achieve 80% power for detecting a one unit difference in the Oucher score, which has a reported standard deviation of 1.5, we would need to sample 36 patients in each group.
Healing time is a more difficult endpoint to assess. Medical textbooks cite that the healing time for second degree burns has a range of 4 days (minimum 10, maximum 14). A study of healing times for a glove made from one of the skin barriers showed a healing time range of 6 (minimum 2 and maximum 8 days).
A rule of thumb is that the standard deviation is about one fourth to one sixth the size of the range. So we could have a standard deviation as small as 0.67 or as large as 1.5. An average change of one day in healing time would be considered clinically relevant.
If we use the largest possible estimate of standard deviation, we would get (coincidentally) the exact same sample size of 36 per group. If we used the smallest estimate of the standard deviation, we would need only 7 subjects per group.
For one type of skin barrier, a study of costs showed a range of $4.00 ($5.50 to $9.50). We would like to be able to detect a difference as small as $0.50 in costs.
Using the same rule of thumb, we get an estimate of the standard deviation of either 0.67 or 1.0. Using the smaller estimate of standard deviation, we would need 29 subjects per group using the smaller estimate of standard deviation. We would need 63 subjects per group, using the larger estimate.
A sample size of 63 is untenable, so we decide that we can live with a study that could only detect a $1.00 change in costs. For this size difference, we would need 16 subjects per group using the larger standard deviation.
In summary, to achieve adequate power for all three endpoints, we would need 36 patients per group,. This is larger than we need for the healing time endpoint. It is also larger than what we need for the cost endpoint, unless we wanted to detect a $0.50 change in costs. To detect such a small difference, we need a sample size of 63 subjects per group.
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