The patients were included after confirmation of the inclusion and exclusion criteria by one of the orthopaedic surgeons responsible for the study (H.N., E.S., or S.P.). All patients gave informed oral and written consent before inclusion. The patients were randomized in a 1:1 ratio to the control group or to the intervention group with use of opaque, sealed envelopes in blocks of ten, stratified for each hospital. The envelopes were then mixed, consecutively numbered, and put in a box. The treating orthopaedic surgeon, other medical staff, and the study team (except for the nurse responsible for conducting the smoking cessation program) were blinded to the allocation. Two study nurses were involved at each hospital: one was responsible for inclusion of the patients and for evaluation of the outcomes and was blinded to the randomization, and the other was responsible for randomization and the smoking cessation intervention. All nurses had had a long experience with randomized clinical trials and were highly aware of the importance of blinding. To further ensure blinding, all patients were asked not to reveal their randomization group, or to discuss it, with the nurse responsible for the outcome assessment or with the staff responsible for the fracture treatment. Both groups received medical and surgical treatment according to the routines in the hospital departments.
Nurses specifically trained to carry out the chosen smoking cessation program17 contacted the included patients on the orthopaedic wards and performed the randomization. The program, initiated within two days during the initial hospitalization period, included one or two personal meetings and weekly telephone contacts for six weeks with the nurse. At the first meeting, the Fagerström score18 was assessed in order to estimate the degree of nicotine dependence and to help plan the smoking cessation program. The patients were continuously encouraged not to smoke, and free nicotine substitution was offered to those who needed it. No other drug therapy was used. The intervention was aimed primarily at keeping the patients from smoking for the first six postoperative weeks. The control group received general advice to stop smoking, but no additional support was offered.
All patients were followed by the study nurses at two to three weeks with a face-to-face meeting, at four weeks with a telephone interview, and at six to twelve weeks with a face-to-face meeting. The time range of six to twelve weeks for the final follow-up visit was chosen for the practical reason that it could be conducted simultaneously with the follow-up evaluation of fracture-healing. The study nurses responsible for recording the complications at each hospital received the same training in how to define and record possible complications on the case record form. A questionnaire regarding the patients’ current smoking status was completed by the patients at the two to three-week and six to twelve-week follow-up visits.
The primary outcome was defined as the number of patients with at least one postoperative complication at six to twelve weeks. Postoperative complications, which were predefined in the study protocol, consisted of any unexpected event causing additional medical or surgical treatment, additional investigations (radiography or laboratory tests), a prolonged hospital stay, or unscheduled postoperative check-ups in the outpatient department19,20. The complications recorded for our patients are listed and defined in Table II.
All complications were verified with a review of the medical records and case record forms by two of the orthopaedic surgeons responsible for the study (H.N. and S.P.) together with an orthopaedic surgeon who was not involved in the study. This review was done after the study was finished and before the randomization code was broken.
Our initial power calculation was based on the results of a previously published randomized clinical trial on a smoking cessation intervention for patients undergoing elective hip and knee surgery12. That study showed a 65% relative risk reduction in postoperative complications, which were assessed until the patient was discharged from the hospital (assessment only until discharge most likely resulted in a complication rate that was lower than it would have been had it been recorded for a longer period21). Making a conservative estimate for our trial, we planned to include 586 patients in total in order to identify a 30% reduction in the complication rate (from 30% to 21%) with a statistical power of 80% (β = 0.20) at the significance level (α) of 0.05. The power calculation was performed with a two-tailed test.
During the study period, it became clear that enrolling patients was more difficult than had been expected. Only about 12% of our patient population smoked, and many were not willing to quit at the time of an acute injury. A major reason for the enrollment slowing down was the introduction of a nonsmoking policy at the participating hospitals, which probably, as a result of an increased awareness of the negative effects of smoking, negatively affected the patients’ interest in participating in a study. As a result of the unexpectedly slow inclusion, a post hoc power analysis was conducted in December 2006, and it was concluded that there was a 40% possibility of detecting a 9% absolute difference (a 30% relative risk reduction) between the groups among the 105 patients already in the study. Furthermore, the analysis showed that the power would remain low until about 500 patients had been included. In spite of the low power, the study enrollment was terminated since it was not likely that it was going to be finalized as planned during a reasonable period of time. No interim analysis was done.
Primary analyses were performed according to the intention-to-treat principle—i.e., the patients included in the study were analyzed according to their original allocation (to the intervention or control group) regardless of whether or not they reported total smoking abstinence during the treatment period. We used the chi-square test to compare the intervention and control groups with regard to nominal values, and we used the Mann-Whitney U test to compare them with regard to ratios and interval values. The results were regarded as significant if p was <0.05 (two-tailed). We also calculated the number of patients who needed to be treated for one patient to benefit from the intervention compared with a control.
A secondary analysis was performed with use of an exact binary logistic regression, which is a viable alternative to the asymptotic logistic regression for analyzing small data sets or when the number of positive or negative events is low22. The probability of a complication occurring was the dependent variable. Predictor variables for the analysis were age, sex, socioeconomic status, American Society of Anesthesiologists score23, number of pack-years (a pack-year is defined as twenty cigarettes per day per year), current diseases, and the randomization group. Due to the large number of variables, the small number of cases, and the lack of prior knowledge of the degree of association between baseline factors and the primary outcome, forward selection was used to decide on a model. Age was regarded as a clinically relevant prognostic factor; hence, it was included in the first step of the selection process, as was the randomization group. A p value of <0.05 was used as an inclusion criterion.
Source of Funding
This study was supported in part by the Stockholm County Council Research Fund and the Swedish National Institute of Public Health. Pfizer financed the nicotine replacement therapy. None of the supporters took part in the design or conduct of the study; in the collection, management, analysis, or interpretation of the data; or in the preparation, review, or approval of the manuscript.
A total of 298 eligible patients were asked to participate in the study (Fig. 1); 105 patients (35%) were enrolled and also randomized, eleven (4%) did not meet the inclusion criteria at the final assessment (e.g., the surgery had been canceled or delayed), and 182 (61%) declined to participate. All randomized patients were followed according to the study protocol, and all but four of the 182 who had declined to otherwise participate agreed to a follow-up by a review of their medical records.
The 298 patients belonged to the total population of about 4800 patients who had fracture surgery performed at the participating departments during the study period and of whom 12% were smokers (according to the hospital databases). The expected prevalence of smokers in Sweden is 14%24,25 and, if adjusted26 for age, the expected prevalence of smokers in our population would be 11%, indicating that our register data are fairly valid. On the basis of these data, we estimated that 18% of all smokers were included, 32% declined to participate, and 50% did not meet the inclusion criteria.
Primary Outcome According to Intention-to-Treat Analysis
As shown in Table II, the proportion of patients who had a postoperative complication was significantly higher in the control group than it was in the intervention group (38% and 20%, respectively; p = 0.048). Superficial wound infection was the most frequently recorded complication, followed by complications related to the plaster cast. Both were more common among the controls, but these individual differences were not significant. There were few serious adverse events—i.e., no deep infections occurred—but a deep venous thrombosis developed in two patients in the control group and a pulmonary embolus developed in one patient in that group. The development of more than one postoperative complication was also more common among the controls (Table III).
The number of patients needed to treat to prevent one patient from having one or more complications was 5.5.
Secondary Outcomes and Analyses
The secondary analysis showed that the exact odds of having a complication were 2.51 times (95% confidence interval, 0.96 to 6.9 times) higher in the control group than in the intervention group, but this difference was not significant.
Twenty-four of forty-eight patients in the intervention group and nine of fifty-two in the control group reported total abstinence from smoking at two weeks (p = 0.001). The corresponding numbers at six weeks were nineteen of forty-four and ten of fifty-one (p = 0.013). The per-protocol analysis did not reveal any significant relationship between the self-reported total abstinence from smoking and the complication rate.
Analysis of the Outcomes for the Nonparticipants
We were able to use medical records to follow 167 of the 182 patients who declined to otherwise participate in the study. Seventy (42%) of these 167 nonparticipants had had at least one complication, and seven of them had had a deep wound infection. There were no significant differences between the nonparticipants and the controls regarding the frequency of postoperative complications. We had no information regarding whether the nonparticipants continued to smoke during the study period.
The main and novel finding of our study is that a six-week smoking cessation program started immediately after emergency fracture surgery significantly reduced the postoperative complication rate. There is convincing evidence that smokers have a generally increased risk of postoperative complications. Randomized studies have shown that a smoking cessation intervention introduced prior to elective surgery significantly reduces the rate of postoperative complications12,13. However, to the best of our knowledge, this is the first randomized controlled trial showing that smoking cessation intervention starting in the acute hospitalization period after an acute injury and continued for a short period of six weeks is sufficient to decrease the number of postoperative complications. The proportion of patients who experienced a postoperative complication was significantly higher in the control group than it was in the intervention group. The development of more than one complication was also more common among the controls. However, our secondary regression analysis could not confirm a significant difference between the groups, although the exact odds of having a complication were 2.51 times lower in the intervention group. The low number of patients that needed to be treated (5.5) to prevent one patient from having one or more complications also indicates a strong effect of the treatment.
We were not able to confirm whether a patient had quit smoking completely, smoked less, or continued smoking as before, which is a difficulty also noted previously by others27,28. However, according to self-reports, a significantly larger number of the patients in the intervention group did quit smoking totally during the study period. It is not unlikely that patients in the control group also smoked less, which could explain the discrepancy between the results of the intention-to-treat analysis and those of the per-protocol analysis. It should also be noted that the intention of our trial was not to evaluate the ability of the intervention to induce patients to quit or decrease smoking but to assess whether the smoking intervention reduced the number of postoperative complications. Compliance with an intervention is probably higher in a trial than it is in clinical practice, but we noticed that some of the patients in the control group also ceased smoking, which suggests that the difference in smoking abstinence between the groups could also be expected in routine health care. The total staff time used for the intervention was less than three hours per patient, indicating that the cost of this well-validated and frequently used intervention17,29 is modest.
In spite of our efforts, we succeeded in including only 18% of all smokers who had fracture surgery performed at the participating departments, which probably reflects a “real life” situation of patients in need of acute fracture surgery. It was more difficult to enroll patients than expected. First, only about 12% of our study population were smokers. Second, as expected, many smokers were not willing to quit at a time when they were going to undergo acute fracture surgery. Third, the inclusion rate in our study was rather low, and it declined during the second year. One explanation is that the prevalence of smoking in Sweden decreased from 24% in the 1990s to 14% in 200624,25, and another is that during the study period the participating hospitals introduced a nonsmoking policy, which decreased the patients’ interest in participating in such a study and the chance of being included in the control group. The eleven eligible patients not meeting the inclusion criteria were mostly non-Swedish-speaking persons or patients who were not operated on at all. Patients with a history of alcohol dependency were excluded because they were not considered to be amenable to follow-up within a study. However, it has been shown by others30 that patients with alcohol dependence are interested in stopping smoking and are able to abstain from smoking if offered adequate support.
We chose to include patients with all types of extremity fractures requiring surgery, which might be questioned since fracture treatment and healing vary. However, this choice can be justified since the focus of our study was on the short-term complications and the main problems were assumed to be related to wound-healing, as has been shown with regard to patients treated with elective surgery8,12. Furthermore, we also hoped that it would be possible to generalize our results to a heterogeneous fracture patient population.
The patients who declined to participate must also be considered when interpreting our results. They might have continued to smoke or they could have quit smoking without help. They were older, they had a higher rate of hip fractures than the rest of the cohort, and their complication rate was high. Even though the older age of those who declined to participate could have affected the complication rate, the patients in the control group had approximately the same number of complications as those who declined to participate. These equivalent levels of complications strengthen our conclusion that our assessment of complications among patients participating in the study is valid.
Our primary end point was the total number of patients with at least one complication, a method used previously by others12,13, and our analysis showed a significant difference between the groups. Most of the established postoperative complications were minor, although they were in accordance with definitions (and frequencies) in previous studies12,13,19-21.
One may question whether some of the complications are clinically relevant. However, superficial wound infections, the most common complication noted, must be considered to be of clinical importance. Although minor superficial infections are usually easy to treat and exert a minor impact on the final medical outcome, these infections are more costly than expected and have a negative impact on the patient’s health and well-being31. Skin abrasions and pain caused by the plaster cast were the second most common complication, and they also were more common in the control group. These problems required one or more additional outpatient visits, which was one of the definitions of a complication. The clinical relevance can be debated, but the seven patients with plaster-cast-related problems required a total of fifteen outpatient visits, resulting in unnecessary health-care costs and suffering for the patients. We believe that the relevance of this type of complication should not be discounted.
The strengths of this study are that it was a randomized controlled trial in a multicenter setting and that the intervention and the follow-up were standardized and conducted by well-trained staff. Another strength is that the outcome assessment was conducted in a single-blinded manner by study nurses and regular staff not aware of the randomization groups. The major limitation of the study is the relatively small number of patients. During the study period, it became clear that we were not going to be able to include the 586 patients required according to the original power calculation within a reasonable time frame. Therefore, we chose to terminate the study enrollment. However, although we succeeded in including less than one-fifth of the initially planned number of patients, significant differences between the groups could be detected. The fact that the differences in absolute numbers were substantial—for example, regarding superficial wound infection rates (20% compared with 8%)—is also worth noting. In spite of this study being a randomized trial, we chose to further explore the results by using an exact binary logistic regression analysis, a method specifically developed for small data sets and small numbers of events. Even though the exact odds of having a postoperative complication were 2.51 times higher in the control group, this finding was not significant. Despite this, our interpretation is that the primary and secondary outcomes added together indicate that there was a difference in the complication frequency between the groups.
The large number of patients who declined to participate in our study is also a weakness and could indicate that a large proportion of smokers may not be reachable for any kind of smoking intervention. On the other hand, 60% to 80% of all smokers are known to want to quit smoking and have made one or more attempts24,32. It is possible that the randomized controlled study setting made the patients hesitate to participate. Therefore, it is likely that a higher percentage of smokers with acute injuries could be reachable if the smoking cessation program were to be offered as part of a clinical routine.
We concluded that our results indicate that this type of smoking cessation program, requiring a total of two to three hours of support from a nurse with adequate training, decreases the risk of early postoperative complications. Therefore, we believe that smokers with an acute fracture requiring emergency surgery should be offered a smoking cessation intervention during the hospitalization period after the injury.
NOTE: The authors would like to express their gratitude to Professor Hans Gilljam (Department of Public Health Sciences, Karolinska Institutet) for his contributions to the design and planning of this study; to Associate Professor Jan Tidermark (Section of Orthopaedics, Department of Clinical Science and Education, Södersjukhuset, Karolinska Institutet) for the contribution of his clinical judgment; and to the study nurses, Catharina Levander, Elisabeth Skogman, Ingemo Sundberg-Petersson, and Paula Kelly-Pettersson, engaged in this project.
Investigation performed at the Department of Clinical Science and Education, Södersjukhuset, Karolinska Institutet, Stockholm, Sweden
Disclosure: In support of their research for or preparation of this work, one or more of the authors received, in any one year, outside funding or grants in excess of $10,000 from the Swedish National Institute of Public Health and the Stockholm County Council Research Fund and of less than $10,000 from Pfizer. In addition, one or more of the authors or a member of his or her immediate family received, in any one year, payments or other benefits in excess of $10,000 or a commitment or agreement to provide such benefits from a commercial entity (Bactiguard AB).
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