Inferences about the effects of treatments – including surgical treatments – rely on making comparisons. These comparisons may be with patient’s symptoms before a treatment has been applied. For example, the return of hearing after puncturing the ear drum (tympanotomy) in certain kinds of longstanding deafness can be so dramatic that the change can be confidently ascribed to the treatment (Cooper 1801; Burton 2015). More usually, treatments have much more modest effects, and alternative treatments may differ from each other only slightly, if at all. In these circumstances disagreements are common about treatment effects, including mechanisms, the magnitude of any effects and the value of a particular treatment. Examples include disputes about different ways of treating wounds (Hidalgo 1604; Solis 2011), the timing and methods of limb amputations (Monro 1737; Bilguer 1764; Alanson 1782; Hunter 1794; Guthrie 1815; Hutchinson 1817), and about lithotripsy as an alternative to lithotomy (Cheselden 1740; Poisson et al 1835; Troehler 2013).
Reducing biases in assessing the effects of surgery
Obtaining reliable estimates of treatment effects, especially when differences between the active and control treatment are moderate, requires the effects of treatments to be distinguished from placebo effects, the effects of biases and the play of chance – in other words, to ensure that comparisons are fair. Of the many biases that can lead to unreliable estimates of the effects of treatments, there are two in particular that researchers have attempted to reduce over the past century.
The first of these – allocation bias – results when the patients in treatment comparison groups differ in prognosis, so that it is impossible to assess whether any differences in outcomes following treatment are due to differential effects of the treatments they have received, or differences in their prognoses before treatments were given. Towards the end of the 19th century, prospective, alternate allocation to treatment comparison groups was introduced to generate groups of patients with similar prognoses (Chalmers et al. 2011). Surgeons were among those who contributed to this methodological development (Keith 1878; Hill 1879; Webster Fox 1894; Langton 1899), which, half a century later, led on to the adoption of concealed random allocation to treatment comparison groups (Medical Research Council 1948; Chalmers 2010; Chalmers et al. 2011).
The second of the two key biases – observer bias – is likely when knowledge of treatment allocation may influence the way that treatments are administered and their possible effects measured. This bias was recognised to be a problem and steps taken to reduce it towards the end of the 18th century. A Royal Commission in Paris used blindfolds to assess whether, as claimed by Anton Mesmer, a force he had dubbed ‘animal magnetism’ was real (Lavoisier 1784; Commission Royale 1784; Donaldson 2016). A few years later, William Haygarth compared the effects of metallic ‘tractors’ with sham, wooden ‘tractors’ in patients with arthritis (Haygarth 1800).
These studies helped to make clear that patients’ expectations and perceptions could result in ineffective treatments being deemed effective. The need for blinding and placebo controls may be debatable if outcome measures are objective – mortality, for example. However, when outcome measures are subjective and reflect satisfaction with the treatment in domains important to patients, such as pain, function, and quality of life (Ware 1993), comparisons of treatments believed to be ‘active’ with sham/placebo treatments are important to reduce biased estimates of treatment effects (Gøtzsche et al. 2004; Wood et al. 2008; Savovic et al. 2012; Wartolowska et al. 2014).
This bias may be caused by patients’ expectations of treatment effects and what they were told to expect from the treatment. They may report symptoms based on their “hunches” about treatment being effective or give answers they believe are “correct” or expected from them, for example, because it would be regarded as impolite not to report improvement. (Sackett 2007; Hrobjartsson et al. 2014).
Blinding means concealing the treatment allocation from patients and any other people (assessors or researchers collecting data, caregivers, data analysts) involved in the trial who may bias the results of the trial by knowing the group to which patients have been allocated. Blinding also improves patient retention in trials. Across the trials we reviewed the withdrawal rate was low (4%) and comparable between the treatment and the placebo arm (Wartolowska et al. 2016). Blinding of patients may also reduce adherence bias (patients in the control group not following the assigned treatment) and help to prevent “contamination of the control group” (seeking and receiving additional treatment outside the trial). (Hrobjartsson et al. 2014).
Although designing and carrying out unbiased controlled trials of surgical treatments is undoubtedly challenging (Fairbank 1999), failure to take steps to reduce observer biases in surgical trials results in untrustworthy estimates of treatment effects (Wartolowska et al. 2016).
A few examples of sham/placebo treatments in the 1950s
Although adoption of blinding and use of placebos in drug trials began in the 19th century (Kaptchuk 2011), these measures were apparently not used in surgical trials until the middle of the 20th century; and even today, surgical comparison groups receiving sham treatments or placebos remain rare (McLeod 1999; Wente et al. 2003; Ergina et al. 2009; Cook 2009).
The earliest example of the use of sham/placebo treatments in surgical research, of which we are aware, is a little known psychosurgical study reported in 1953 (Livingston 1953). Some patients with psychoses underwent anterior cingulate cortex isolation (excision of a part of cingulum), but four patients had only a skin incision and removal of a fragment of skull bone without any intervention to alter brain anatomy. None of the patients who had had placebo treatment improved and all of them subsequently underwent excision of a fragment of cingulum.
Better known early placebo controlled trials of surgical treatment compared the effects on angina of internal mammary artery ligation with an inactive procedure consisting of bilateral skin incisions without actual artery ligation in patients with angina (Cobb et al. 1959; Dimond et al. 1960). The symptoms, function (exercise tolerance) and medication (use of nitroglycerin) of patients in the ligation and the sham groups improved to similar extents. The improvement was attributed to patient interaction with the surgeon, the surgeon’s personality, participation in the treatment, alleviation of anxiety, and spontaneous improvement (Cobb et al. 1959; Dimond et al. 1960).
Use of sham/placebo treatments during the 1980s and 1990s
These early trials in the 1950s studied few patients, who were not informed that some of them would receive a placebo intervention. As was noted by Thomsen and colleagues in 1981, “knowledge of the possibility of having a purely placebo operation probably reduces the efficacy also in the actively treated group, and the outcome of the trial will be equivocal” (Thomsen et al. 1981). In their trial of treatment for Menière’s disease, half of the patients underwent an endolymphatic sac shunt operation, while the other half underwent regular mastoidectomy. The patients were told that the trial was comparing two different operations that were believed to be equally effective (Thomsen et al. 1981). Thomsen and his colleagues recognised the need to blind patients and investigators when subjective outcomes were being used to assess treatment effects: “In dealing with a disease or a syndrome like Menière’s disease, with its fluctuations in intensity of symptoms, spontaneous remission of symptoms, etc., open, uncontrolled studies are without any value in testing a treatment modality, be it medical or surgical. (…) The double-blind technique therefore is an absolute necessity in such investigations, and any leak in the blind must be considered disastrous” (Thomsen et al. 1981).
The advent of minimally-invasive surgical techniques and scopes opened up new possibilities for blinding in surgical trials. A skin incision imitating open surgery was no longer necessary because using a scope meant that there was either no visible surgical wound in the case of endoscopy or bronchoscopy, or only a small incision after laparoscopy or arthroscopy. For example, in trials of interventions to treat bleeding oesophageal varices (Fleisher et al. 1985; Hartigan 1994), peptic ulcers (MacLeod et al. 1983; Freitas et al. 1985), and endometriosis (Sutton et al. 1994) all patients underwent endoscopy or laparoscopy but only some patients had an additional active procedure to help secure haemostasis or remove the lesions. Other investigators used endoscopy to insert intragastric balloons in trials of surgical treatments for obesity (Lindor et al. 1987; Meshkinpour et al. 1988; Mathus-Vliegen et al. 1990).
Increased use of placebo controlled surgical trials in the 21st century
By the beginning of the current century the importance of blinding in assessing the effects of surgical treatments had become more widely accepted and there has been a rapid increase in the number of placebo-controlled surgical trials. Some of these trials have sparked heated debates about the role and ethical aspects of placebos in assessing surgery, for example, the trials to assess the effects of dopaminergic neurone transplants in patients with advanced Parkinson’s disease (Freed et al. 2001; Olanow et al. 2003; Gross et al. 2011). These studies used a skin incision and burr holes in the skull as well as several additional diagnostic and therapeutic procedures, some of them clinically necessary and some performed to maintain blinding. For example, patients in both study arms underwent magnetic resonance imaging and positron emission tomography scans (Freed et al. 2001), or received drugs to prevent rejection of the transplanted cells (Olanow et al. 2003) or to prevent epilepsy after the transplantation procedure (Freed et al. 2001).
Placebo controlled trials undertaken to assess the effects of arthroscopic debridement (Moseley et al. 2002) or tidal irrigation (Bradley et al. 2002) in patients with knee osteoarthritis have also been controversial. The blinded trial reported by Moseley and colleagues failed to detect the beneficial effects suggested by the results of earlier, unblinded trials of debridement (Merchan and Galindo 1993) and lavage (Ike et al. 1992).
Increasing use of implants to change anatomy, and lasers or other energy-emitting devices to alter tissues has meant that, in some cases, it has been possible to blind surgeons. For example, in a study reported by Freeman and colleagues (2006), the surgeon inserted a catheter under fluoroscopic guidance and handed over the subsequent procedure to a technician who delivered or did not deliver the radio-frequency energy. In other trials, the delivery system for palatal implants to reduce obstructive sleep apnoea was prepared by the manufacturer to either contain the implant or not, so that surgeons did not know whether they had performed an actual implantation or a sham procedure (Gillespie et al. 2011; Maurer et al. 2012).
Increasingly sophisticated efforts to maintain blinding in surgical trials
Preparation for the sham/placebo procedure has usually been done as it has as for the active procedure. Steps have been taken to imitate visual, auditory and physical cues (Moseley et al. 2002; Pauza et al. 2004; Kallmes et al. 2009; Kapural et al. 2013). To mimick sounds, surgeons have been required to talk through the steps of the procedure (Rothstein et al. 2006), to ask for the instruments (Koutsourelakis et al. 2008; Sihvonen et al. 2013), to use suction (Sihvonen et al. 2013), or ask for a laser or other device to be activated, although it was not used in the placebo group (Fleischer 1985; Mathus-Vliegen et al. 1990; Nease and Krempl 2004; Leon et al. 2005; Roehrborn et al. 2013).
Both the people performing interventions and endoscopic images have been screened from patients (Salem et al. 2004), either using a surgical drape (Roehrborn et al. 2013) or by arranging the operating room in such a way that the patient could not see the procedure (Kapural et al. 2013). In one trial patients were heavily sedated and required to wear dark goggles (Stone et al. 2002).
Surgeons also attempted to imitate sensory cues, for example, by manipulating the knee as if an actual arthroscopy was being performed (Sihvonen et al. 2013), injecting saline during tidal irrigation (Bradley et al. 2002), or by splashing saline on the knee to simulate lavage (Moseley et al. 2002). In a trial of meniscectomy, surgeons used a mechanized shaver (without the blade) pushing it firmly against the patella to simulate the sensations the patient would experience during the surgery (Sihvonen et al. 2013). In a trial of intragastric balloon insertion for obesity, operators manipulated the endoscope as it would be manipulated during the balloon insertion and created the sensation of resistance in the stomach (Mathus-Vliegen et al. 1990).
Even smell during the surgery was imitated to make the placebo procedure indistinguishable from surgery. For example, in the trial by Deviere and colleagues there were concerns that patients could have known the allocation because the copolymer used in the active arm had a distinct smell (Deviere et al. 2005). Therefore, in trials of vertebroplasty, a container with cement was opened during the placebo procedure to help with blinding (Kallmes et al. 2009; Buchbinder et al. 2009).
Reports of several trials stated that the duration of procedures in the surgical and the control arms was matched, either by imitating the elements of the surgical procedure or by keeping all patients in the operation room for the same length of time (Moseley et al. 2002; Montgomery et al. 2006; Koutsourelakis et al. 2008; Castro et al. 2010; Gross et al. 2011; Sihvonen et al. 2013; Eid et al. 2014). In some trials, however, the placebo procedure was shorter than the surgical intervention, because it was judged unethical to prolong placebo treatment (Fleischer 1985; Deviere et al. 2005).
Most trials blinded assessors but the surgeon and other staff in the operating room were made aware of the group assignment; however, they did not participate in further treatment, post-operative care or follow-up of the patient (Abbott et al. 2004; Sihvonen et al. 2013; Cotton et al. 2014). In a trial by Thomsen, the post-operative care and assessment was done at a different hospital from the surgery (Thomsen et al. 1981). The trial by Cotton and colleagues provided blinded post-operative care by referral to physicians (who were blinded when deciding on treatment) and when this was not sufficient, by an evaluating physician at the study site (who was also blinded) (Cotton et al. 2014).
The importance of placebo controlled surgical trials
Comparisons of surgical treatments believed to be ‘active’ with sham/placebo treatments are important because they reduce biased estimates of treatment effects (Wartolowska et al. 2016). Although double-blind randomized trials are costly and often difficult to perform, their cost is a fraction of the costs to patients and health services of ineffective, invasive and harmful treatments.
Half a century after surgeons and others began to recognise the value of placebo controlled trials of surgery (Thomsen et al. 1981) there are still no regulations requiring surgical procedures to be shown to be efficacious and safe as there are for drugs. The consequence is much unjustified surgery being used at inevitable risk to the wellbeing of patients and expense to health services. Sixty-six placebo-controlled trials in surgery were reported in the first 15 years of the 21st century compared with only 19 during the whole of the second half of the 20th century. This recent increase in the use of placebo controlled trials of surgery is an encouraging sign that biased estimates of the effects of surgical treatment are being recognised and addressed.
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