- Email: [email protected]
Five easy pieces on evidence-based medicine (2)
European Journal of Pain (2000) 4: 321–324 doi:10.1053/eujp.2000.0191, available online at http://www.idealibrary.com on
Evidence-based medicine
Five easy pieces on evidence-based medicine (2) Eija Kalsoa and R. Andrew Mooreb a
Pain Clinic, Department of Anaesthesia and Intensive Care Medicine, Helsinki University Hospital, Helsinki, Finland; bPain Research and Nuffield Department of Anaesthetics, University of Oxford, Oxford Radcliffe Hospitals, The Churchill, Oxford, UK.
WHY RANDOMIZED AND (PLACEBO) CONTROLLED? The highest quality clinical trials are those that are randomized and double-blind. Studies, however, can be both randomized and double blind, and still be invalid because they cannot show what they set out to. One of the most contentious issues is the use of placebo. Are these concepts important only for the elite researchers or should they be taken seriously by the clinicians, too. Let’s have a look!
Why randomized? Selection bias is best controlled by allocating patients at random to the different study groups. Each patient should have the same probability of being included in each comparison group and the allocation should be concealed, preferably until the study is completed. Randomization should not be based on date of birth or anything that will enable the person in charge of allocation to steer the process in a desired direction. Ideally, randomization is performed by someone who has no direct relationship to the study participants using tables of random numbers or numbers generated by computers. Proper randomization is essential as Correspondence to: Eija Kalso, Pain Clinic, Department of Anaesthesia and Intensive Care Medicine, Helsinki University Hospital, P.O. Box 340, FIN-00029 HUS, Finland. E-mail: [email protected]
inadequate concealment of treatment allocation overestimates the treatment effect by 41% (Schultz et al., 1995). Non-randomized studies can give the wrong answer (Carroll et al., 1996). Why double-blind? Double-blinding is achieved if at least the study subject and those making the observations are unaware of the treatment. Lack of doubleblinding will overestimate the treatment effect by roughly 17% (Schulz et al., 1995). Again, lack of double-blinding can lead to completely different answers, as with acupuncture in back pain (Ernst and White, 1998). Double-blinding may be difficult to achieve if the studied treatment is invasive and if the subjects and observers can decode blinding because of e.g. adverse effects. Blinding can be tested by asking the subjects and observers which treatment they thought was given. What does the control group tell us? The control group should aid us in finding out what would happen to the patients if they had no treatment (what is the natural course of the disease) and/or how the new treatment compares with an established treatment, should there be one. Table 1 shows a hypothetical construction of various aspects that may be involved in the control group. Often we are unclear about important issues, like the natural course of disease (including disease severity), and we certainly know little
1090-3801/00/030321 + 04 $35.00/0 © 2000 European Federation of Chapters of the International Association for the Study of Pain
322
E. K ALSO
TABLE 1. 1. 2. 3. 4.
R. A. M OORE
Sum of effects in the control group
Waiting list = natural course – negativity as nothing is being done Visits without treatment = natural course + doctor/nurse and patient interaction Placebo treatment = natural course + interaction + expectation that there will be an effect Active control = natural course + interaction + expectation + actual effect
TABLE 2. 1. 2. 3.
AND
Common misconceptions about placebo
A fixed fraction of the population responds to placebo The extent of the placebo reaction is a fixed fraction being about one third of the maximum possible The more invasive the method the greater the placebo effect is (injections produce a greater placebo effect than tablets)
about much else in this complicated process. The point about randomized, double-blind placebocontrolled trials is that they allow us to tease out the actual effect of a treatment. Most of the clinical trials in pain research are performed on drugs. Ideally, the protocol should include an inactive control (placebo), an active control and the study drug in more than one dose. This means several groups and large numbers of patients need to be recruited. If we can afford only three groups, these should be placebo, active control and study drug. What if an ethics committee suggested that omitting the placebo group would be unethical? You could compare the new analgesic with a standard analgesic like morphine or paracetamol. At the end of the study the statistics would probably indicate that the treatments are equally effective. Could you argue that the new drug you studied is as effective as morphine? You could, but the counter argument would be that your study was unable to detect any difference. Studies to demonstrate unequivocally that there was no difference would have to be very large; many times greater than a standard analgesic study. But you don’t know that the new drug and morphine or paracetamol would have been as good as placebo had it been included in the study. This is not an uncommon occurrence. Your particular study may have been insensitive, and the ability to demonstrate sensitivity would have been lost by excluding the placebo group. So the study would, in reality, have told you nothing, because even the conclusion that it was about as effective as morphine or paracetamol would be flawed (McQuay and Moore, 1996). European Journal of Pain (2000), 4
About the placebo effect The placebo effect is intriguing and it may be particularly important in studies on pain. The most common misconceptions about placebos are listed in Table 2. Beecher (1955) originally proposed that about a third of people responded to placebo and Evans (1974) stated that the placebo effect was a fixed fraction of the active, again about a third. Both are wrong. Table 3 shows data on the different placebo response rates across studies in different conditions over different follow up times. The variation is 12–40%. It also seems that the response rate with placebo is lower if the outcome is tougher, for instance pain free at 2 h after treatment for migraine compared with moderate to severe pain reduced to no pain or mild pain. We should not jump to the conclusion that placebo is causing these improvements, but rather we may be measuring a number of effects, including the natural course of the disease. The natural course of the pain condition may be more favourable in diabetic neuropathy as compared with postherpetic neuralgia, for instance. McQuay et al. (1995b) confirmed that the mean placebo scores were related to the mean score for the active treatments in each study. This relationship disappeared when median values were used. This was explained by the fact that patient responses are not normally distributed. The median placebo response (fraction of patients having at least 50% pain relief with placebo) in studies on acute postoperative pain is 2–14%.
E VIDENCE - BASED
TABLE 3.
323
MEDICINE
Placebo responder rates in different pain conditions.
Condition
Treatment
Outcome
Duration of study
Number of patients
% of placebo responders
Acute postoperative pain (Moore, 2000) Strains and sprains (Moore et al., 1998) Migraine (Oldman et al., 2000) Migraine (Oldman et al., 2000) Trigeminal neuralgia (McQuay et al., 1995a) Diabetic neuropathy (McQuay et al., 1996) Postherpetic neuralgia (McQuay et al., 1996) Atypical facial pain (McQuay et al., 1996) Dysmenorrhoea (Zhang & Li Wan Po, 1998)
Analgesics
At least 50% pain relief At least 50% pain relief No pain/mild pain Pain free
4–6 h
12 000
18
7 days
12 500
40
2h
5000
29
2h
800
10
At least 50% pain relief At least 50% pain relief At least 50% pain relief At least 50% pain relief At least 50% pain relief
3–6.5 months 3–6.5 months 3–6.5 months 3–6.5 months About 1 day
224
18
200
36
68
12
85
35
1607
22
Topical NSAIDs Migraine analgesics Migraine analgesics Antiepileptics Tricyclic antidepressants Tricyclic antidepressants Tricyclic antidepressants Minor analgesics
The third point is also wrong. The overall response to oral placebo in 12 000 patients enrolled in acute pain trials was 18% having at least 50% pain relief (Moore, 2000). The figure for injected morphine was 16% in identical patients in identical trials with identical outcomes (McQuay et al., 1999).
Placebos: an important ethical question Placebos have also ignited ethical disputes. A recent study on paediatric pain is an example. Korpela et al. (1999) studied the effectiveness of different doses of rectal paracetamol in paediatric day-case surgery. The Editor-in-chief of one journal rejected it without sending it to referees because the study was too unethical. A second journal accepted it avidly. The ethically questionable aspects were that the children were not given opioids before or during surgery, that a placebo group was included, and that high doses of paracetamol were given. Because of this study design a beautiful dose response for escalating doses of paracetamol could be demonstrated because there was enough baseline pain. Ten percent of the children who were given placebo at the beginning of anaesthe-
sia instead of one of the three doses of paracetamol (20, 40 or 60 mg/kg) did not need any pain killers during the 2 h follow up, even though the children were not given opioids during anaesthesia. The lowest dose of 20 mg/kg was no different from placebo. It is possible to argue that it was unethical to recommend doses of paracetamol (10–15 mg/ kg) for the children that were ineffective, as the ED50 of rectal paracetamol is 35 mg/kg. It is possible to argue that the placebo group was unnecessary as the three different doses of paracetamol showed a dose response. However, these are post hoc arguments. Had there been no difference between the groups, one could not have known the reason for this. Most probably the reason would have been that the study had been insensitive if opioids had been administered during surgery and the children would have had very little baseline pain. This might have been good clinical practice but the study would have failed to provide any answers and children would have been given too low doses of paracetamol in the years to come. To some extent, patients participating in clinical trials are being altruistic. They take a chance so that future patients can have a certainty. Clinical studies must, therefore, be able to European Journal of Pain (2000), 4
324
answer clinical questions or they are themselves unethical (Tramèr et al., 1998). In pain, placebo groups are acceptable if certain rules are followed: the patient must have given informed consent, effective escape medication must be readily available and the patient must be able to quit the study whenever he/she feels like it. There are also areas where placebos cannot be used: cancer patients who are already on opioids cannot be randomized to a placebo group. In short, use of placebo controls in conditions for which effective treatment exists is ethical—provided that the use of placebo for the duration of the study does not place the patient at increased risk of irreversible harm or cause unacceptable discomfort. So randomization and use of placebo controls, in the end, can be the main determinants of how every clinician chooses to use or not to use a therapy. The alternative is voodoo medicine.
REFERENCES Beecher HK. The powerful placebo. JAMA 1955; 159: 1602–1606. Carroll D, Tramèr M, McQuay H, Nye B, Moore A. Randomization is important in studies with pain outcomes: Systematic review of transcutaneous electrical nerve stimulation in acute postoperative pain. Br J Anaesth 1996; 77: 798–803. Ernst E, White AR. Acupuncture for back pain: A metaanalysis of randomised controlled trials. Arch Int Med 1998; 158: 2235–2241. Evans FJ. The placebo response in pain reduction. In: Bonica JJ, editor. Advances in Neurology, Vol 4. New York: Raven Press; 1974: 289–296. Korpela R, Korvenoja P, Meretoja O. Morphine-sparing effect of acetaminophen in pediatric day-case surgery. Anesthesiology 1999; 91: 442–447.
European Journal of Pain (2000), 4
E. K ALSO
AND
R. A. M OORE
McQuay H, Carroll D, Jadad AR, Wiffen P, Moore A. Anticonvulsant drugs for management of pain: a systematic review. Br Med J 1995a; 311: 1047–1052. McQuay H, Carroll D, Moore A. Variation in the placebo effect in randomsied controlled trials of analgesics: all is as blind as it seems. Pain 1995b; 64: 331–335. McQuay H, Moore A. Placebo mania. Placebos are essential when extent and variability of placebo response are unknown. Br Med J 1996; 313: 1008. McQuay HJ, Tramèr M, Nye BA, Carroll D, Wiffen PJ, Moore RA. A systematic review of antidepressants in neuropathic pain. Pain 1996; 68: 217–227. McQuay HJ, Carroll D, Moore RA. Injected morphine in postoperative pain: a quantitative systematic review. J Pain Symptom Manage 1999; 17: 164–174. Moore RA, Tramèr MR, Carroll D, Wiffen PJ, McQuay HJ. Quantitative systematic review of topically applied nonsteroidal anti-inflammatory drugs. Br Med J 1998; 316: 333–338. Moore RA. Understanding clinical trials: what have we learned from systematic reviews? Proceedings of the 9th World Congress on Pain, Progress in Pain Research & Management, Vol 16, Eds M Devor, MC Rowbotham, Z Wiesenfeld-Hallin. IASP Press, Seattle, 2000, pp. 757–770. Oldman AD, Smith LA, McQuay HJ, Moore RA. A systematic review and league table of pharmacological interventions for acute migraine attack. Proceedings of the 9th World Congress on Pain, Progress in Pain Research & Management, Vol 16, Eds M Devor, MC Rowbotham, Z Wiesenfeld-Hallin. IASP Press, Seattle, 2000, pp. 603–608. Schultz KF, Chalmers I, Hayes RJ, Altman DG. Empirical evidence of bias: dimensions of methodological quality associated with estimates of treatment effects in controlled trials. JAMA 1995; 273: 408–412. Tramèr M, Reynolds DJ, McQuay HJ, Moore RA. When placebo controls are essential and equivalence trials are inadequate – evidence from a systematic review on ondansetron. Br Med J 1998; 317: 875–879. Zhang WY, Li Wan Po A. Efficacy of minor analgesics in primary dysmenorrhoea: a systematic review. Br J Obstet Gynaecol 1998; 105: 780–789.
Evidence-based medicine
Five easy pieces on evidence-based medicine (2) Eija Kalsoa and R. Andrew Mooreb a
Pain Clinic, Department of Anaesthesia and Intensive Care Medicine, Helsinki University Hospital, Helsinki, Finland; bPain Research and Nuffield Department of Anaesthetics, University of Oxford, Oxford Radcliffe Hospitals, The Churchill, Oxford, UK.
WHY RANDOMIZED AND (PLACEBO) CONTROLLED? The highest quality clinical trials are those that are randomized and double-blind. Studies, however, can be both randomized and double blind, and still be invalid because they cannot show what they set out to. One of the most contentious issues is the use of placebo. Are these concepts important only for the elite researchers or should they be taken seriously by the clinicians, too. Let’s have a look!
Why randomized? Selection bias is best controlled by allocating patients at random to the different study groups. Each patient should have the same probability of being included in each comparison group and the allocation should be concealed, preferably until the study is completed. Randomization should not be based on date of birth or anything that will enable the person in charge of allocation to steer the process in a desired direction. Ideally, randomization is performed by someone who has no direct relationship to the study participants using tables of random numbers or numbers generated by computers. Proper randomization is essential as Correspondence to: Eija Kalso, Pain Clinic, Department of Anaesthesia and Intensive Care Medicine, Helsinki University Hospital, P.O. Box 340, FIN-00029 HUS, Finland. E-mail: [email protected]
inadequate concealment of treatment allocation overestimates the treatment effect by 41% (Schultz et al., 1995). Non-randomized studies can give the wrong answer (Carroll et al., 1996). Why double-blind? Double-blinding is achieved if at least the study subject and those making the observations are unaware of the treatment. Lack of doubleblinding will overestimate the treatment effect by roughly 17% (Schulz et al., 1995). Again, lack of double-blinding can lead to completely different answers, as with acupuncture in back pain (Ernst and White, 1998). Double-blinding may be difficult to achieve if the studied treatment is invasive and if the subjects and observers can decode blinding because of e.g. adverse effects. Blinding can be tested by asking the subjects and observers which treatment they thought was given. What does the control group tell us? The control group should aid us in finding out what would happen to the patients if they had no treatment (what is the natural course of the disease) and/or how the new treatment compares with an established treatment, should there be one. Table 1 shows a hypothetical construction of various aspects that may be involved in the control group. Often we are unclear about important issues, like the natural course of disease (including disease severity), and we certainly know little
1090-3801/00/030321 + 04 $35.00/0 © 2000 European Federation of Chapters of the International Association for the Study of Pain
322
E. K ALSO
TABLE 1. 1. 2. 3. 4.
R. A. M OORE
Sum of effects in the control group
Waiting list = natural course – negativity as nothing is being done Visits without treatment = natural course + doctor/nurse and patient interaction Placebo treatment = natural course + interaction + expectation that there will be an effect Active control = natural course + interaction + expectation + actual effect
TABLE 2. 1. 2. 3.
AND
Common misconceptions about placebo
A fixed fraction of the population responds to placebo The extent of the placebo reaction is a fixed fraction being about one third of the maximum possible The more invasive the method the greater the placebo effect is (injections produce a greater placebo effect than tablets)
about much else in this complicated process. The point about randomized, double-blind placebocontrolled trials is that they allow us to tease out the actual effect of a treatment. Most of the clinical trials in pain research are performed on drugs. Ideally, the protocol should include an inactive control (placebo), an active control and the study drug in more than one dose. This means several groups and large numbers of patients need to be recruited. If we can afford only three groups, these should be placebo, active control and study drug. What if an ethics committee suggested that omitting the placebo group would be unethical? You could compare the new analgesic with a standard analgesic like morphine or paracetamol. At the end of the study the statistics would probably indicate that the treatments are equally effective. Could you argue that the new drug you studied is as effective as morphine? You could, but the counter argument would be that your study was unable to detect any difference. Studies to demonstrate unequivocally that there was no difference would have to be very large; many times greater than a standard analgesic study. But you don’t know that the new drug and morphine or paracetamol would have been as good as placebo had it been included in the study. This is not an uncommon occurrence. Your particular study may have been insensitive, and the ability to demonstrate sensitivity would have been lost by excluding the placebo group. So the study would, in reality, have told you nothing, because even the conclusion that it was about as effective as morphine or paracetamol would be flawed (McQuay and Moore, 1996). European Journal of Pain (2000), 4
About the placebo effect The placebo effect is intriguing and it may be particularly important in studies on pain. The most common misconceptions about placebos are listed in Table 2. Beecher (1955) originally proposed that about a third of people responded to placebo and Evans (1974) stated that the placebo effect was a fixed fraction of the active, again about a third. Both are wrong. Table 3 shows data on the different placebo response rates across studies in different conditions over different follow up times. The variation is 12–40%. It also seems that the response rate with placebo is lower if the outcome is tougher, for instance pain free at 2 h after treatment for migraine compared with moderate to severe pain reduced to no pain or mild pain. We should not jump to the conclusion that placebo is causing these improvements, but rather we may be measuring a number of effects, including the natural course of the disease. The natural course of the pain condition may be more favourable in diabetic neuropathy as compared with postherpetic neuralgia, for instance. McQuay et al. (1995b) confirmed that the mean placebo scores were related to the mean score for the active treatments in each study. This relationship disappeared when median values were used. This was explained by the fact that patient responses are not normally distributed. The median placebo response (fraction of patients having at least 50% pain relief with placebo) in studies on acute postoperative pain is 2–14%.
E VIDENCE - BASED
TABLE 3.
323
MEDICINE
Placebo responder rates in different pain conditions.
Condition
Treatment
Outcome
Duration of study
Number of patients
% of placebo responders
Acute postoperative pain (Moore, 2000) Strains and sprains (Moore et al., 1998) Migraine (Oldman et al., 2000) Migraine (Oldman et al., 2000) Trigeminal neuralgia (McQuay et al., 1995a) Diabetic neuropathy (McQuay et al., 1996) Postherpetic neuralgia (McQuay et al., 1996) Atypical facial pain (McQuay et al., 1996) Dysmenorrhoea (Zhang & Li Wan Po, 1998)
Analgesics
At least 50% pain relief At least 50% pain relief No pain/mild pain Pain free
4–6 h
12 000
18
7 days
12 500
40
2h
5000
29
2h
800
10
At least 50% pain relief At least 50% pain relief At least 50% pain relief At least 50% pain relief At least 50% pain relief
3–6.5 months 3–6.5 months 3–6.5 months 3–6.5 months About 1 day
224
18
200
36
68
12
85
35
1607
22
Topical NSAIDs Migraine analgesics Migraine analgesics Antiepileptics Tricyclic antidepressants Tricyclic antidepressants Tricyclic antidepressants Minor analgesics
The third point is also wrong. The overall response to oral placebo in 12 000 patients enrolled in acute pain trials was 18% having at least 50% pain relief (Moore, 2000). The figure for injected morphine was 16% in identical patients in identical trials with identical outcomes (McQuay et al., 1999).
Placebos: an important ethical question Placebos have also ignited ethical disputes. A recent study on paediatric pain is an example. Korpela et al. (1999) studied the effectiveness of different doses of rectal paracetamol in paediatric day-case surgery. The Editor-in-chief of one journal rejected it without sending it to referees because the study was too unethical. A second journal accepted it avidly. The ethically questionable aspects were that the children were not given opioids before or during surgery, that a placebo group was included, and that high doses of paracetamol were given. Because of this study design a beautiful dose response for escalating doses of paracetamol could be demonstrated because there was enough baseline pain. Ten percent of the children who were given placebo at the beginning of anaesthe-
sia instead of one of the three doses of paracetamol (20, 40 or 60 mg/kg) did not need any pain killers during the 2 h follow up, even though the children were not given opioids during anaesthesia. The lowest dose of 20 mg/kg was no different from placebo. It is possible to argue that it was unethical to recommend doses of paracetamol (10–15 mg/ kg) for the children that were ineffective, as the ED50 of rectal paracetamol is 35 mg/kg. It is possible to argue that the placebo group was unnecessary as the three different doses of paracetamol showed a dose response. However, these are post hoc arguments. Had there been no difference between the groups, one could not have known the reason for this. Most probably the reason would have been that the study had been insensitive if opioids had been administered during surgery and the children would have had very little baseline pain. This might have been good clinical practice but the study would have failed to provide any answers and children would have been given too low doses of paracetamol in the years to come. To some extent, patients participating in clinical trials are being altruistic. They take a chance so that future patients can have a certainty. Clinical studies must, therefore, be able to European Journal of Pain (2000), 4
324
answer clinical questions or they are themselves unethical (Tramèr et al., 1998). In pain, placebo groups are acceptable if certain rules are followed: the patient must have given informed consent, effective escape medication must be readily available and the patient must be able to quit the study whenever he/she feels like it. There are also areas where placebos cannot be used: cancer patients who are already on opioids cannot be randomized to a placebo group. In short, use of placebo controls in conditions for which effective treatment exists is ethical—provided that the use of placebo for the duration of the study does not place the patient at increased risk of irreversible harm or cause unacceptable discomfort. So randomization and use of placebo controls, in the end, can be the main determinants of how every clinician chooses to use or not to use a therapy. The alternative is voodoo medicine.
REFERENCES Beecher HK. The powerful placebo. JAMA 1955; 159: 1602–1606. Carroll D, Tramèr M, McQuay H, Nye B, Moore A. Randomization is important in studies with pain outcomes: Systematic review of transcutaneous electrical nerve stimulation in acute postoperative pain. Br J Anaesth 1996; 77: 798–803. Ernst E, White AR. Acupuncture for back pain: A metaanalysis of randomised controlled trials. Arch Int Med 1998; 158: 2235–2241. Evans FJ. The placebo response in pain reduction. In: Bonica JJ, editor. Advances in Neurology, Vol 4. New York: Raven Press; 1974: 289–296. Korpela R, Korvenoja P, Meretoja O. Morphine-sparing effect of acetaminophen in pediatric day-case surgery. Anesthesiology 1999; 91: 442–447.
European Journal of Pain (2000), 4
E. K ALSO
AND
R. A. M OORE
McQuay H, Carroll D, Jadad AR, Wiffen P, Moore A. Anticonvulsant drugs for management of pain: a systematic review. Br Med J 1995a; 311: 1047–1052. McQuay H, Carroll D, Moore A. Variation in the placebo effect in randomsied controlled trials of analgesics: all is as blind as it seems. Pain 1995b; 64: 331–335. McQuay H, Moore A. Placebo mania. Placebos are essential when extent and variability of placebo response are unknown. Br Med J 1996; 313: 1008. McQuay HJ, Tramèr M, Nye BA, Carroll D, Wiffen PJ, Moore RA. A systematic review of antidepressants in neuropathic pain. Pain 1996; 68: 217–227. McQuay HJ, Carroll D, Moore RA. Injected morphine in postoperative pain: a quantitative systematic review. J Pain Symptom Manage 1999; 17: 164–174. Moore RA, Tramèr MR, Carroll D, Wiffen PJ, McQuay HJ. Quantitative systematic review of topically applied nonsteroidal anti-inflammatory drugs. Br Med J 1998; 316: 333–338. Moore RA. Understanding clinical trials: what have we learned from systematic reviews? Proceedings of the 9th World Congress on Pain, Progress in Pain Research & Management, Vol 16, Eds M Devor, MC Rowbotham, Z Wiesenfeld-Hallin. IASP Press, Seattle, 2000, pp. 757–770. Oldman AD, Smith LA, McQuay HJ, Moore RA. A systematic review and league table of pharmacological interventions for acute migraine attack. Proceedings of the 9th World Congress on Pain, Progress in Pain Research & Management, Vol 16, Eds M Devor, MC Rowbotham, Z Wiesenfeld-Hallin. IASP Press, Seattle, 2000, pp. 603–608. Schultz KF, Chalmers I, Hayes RJ, Altman DG. Empirical evidence of bias: dimensions of methodological quality associated with estimates of treatment effects in controlled trials. JAMA 1995; 273: 408–412. Tramèr M, Reynolds DJ, McQuay HJ, Moore RA. When placebo controls are essential and equivalence trials are inadequate – evidence from a systematic review on ondansetron. Br Med J 1998; 317: 875–879. Zhang WY, Li Wan Po A. Efficacy of minor analgesics in primary dysmenorrhoea: a systematic review. Br J Obstet Gynaecol 1998; 105: 780–789.