On 2016 Nov 05, Peter H. Asdahl commented:

I read with interest the study by Villani et al., who reported findings of a cancer surveillance program among TP53 mutation carriers. The authors analysed data from 89 TP53 mutation carriers diagnosed and followed at three tertiary cancer care centres in North America. Villani et al. concluded that their surveillance program is feasible, detects early tumour stages, and confers a sustained survival benefit. I emphasize a more conservative interpretation of the results because of biases common to observational studies of screening effects.

The primary outcome of the study was incident cancers. If the surveillance and non-surveillance groups were exchangeable at baseline (i.e. had similar distribution of known and unknown factors that affect cancer incidence), we would expect either higher frequency or earlier detection of cancer in the surveillance group because of differential detection attributable to systematic cancer surveillance. The results reported by Villani et al. are counterintuitive: 49% and 88% of individuals in the surveillance and non-surveillance groups, respectively, were diagnosed with at least one incident cancer (crude risk ratio for the effect of surveillance=0.56, 95% confidence limits: 0.41, 0.76. – n.b. risk time distribution is not included in the manuscript). This inverse result suggests that the groups were not exchangeable, and thus confounding is a concern. The potential for confounding is further supported by baseline imbalances in age, sex, and previous cancer diagnosis, which favour higher cancer incidence in the non-surveillance group (the P-values in Table 1 are misleading because of low power to detect differences).

The baseline imbalance between groups is exacerbated by lead time and length time biases when comparing survival. Detection of asymptomatic tumours by surveillance invariably adds survival time to the surveillance group and gives a spurious indication of improved survival. (Croswell JM, 2010) The effects of this bias are well-documented, and depending on the time from detection to symptom onset, the bias may be substantial. The survival analysis is further invalidated by the inclusion of non-cancerous lesions (e.g. fibroadenoma and osteochondroma, which are unlikely to affect survival) and pre-cancerous lesions (e.g. colonic adenoma and dysplastic naevus). Such lesions accounted for 40% and 16% of the incident neoplasms in the surveillance group and non-surveillance group, respectively.

Annual MRI was included in the surveillance protocol. Many of the malignancies among TP53 mutation carriers are rapidly growing, and thus more often detected by symptoms rather than annual follow-up. For example, most medulloblastoma recurrences are detected by symptoms a median of four months after the last imaging. (Torres CF, 1994)

In summary, the study by Villani et al. is not immune to biases common to observational studies of screening effects (Croswell JM, 2010) and the results should not be interpreted as a benefit of surveillance of TP53 mutation carriers as it uncritically has been done by many, which is well described in the accompanying editorial. The benefit, if any, of the proposed surveillance program cannot be assessed without a more rigorous study design to reduce known biases. For example, a study based on random allocation of individuals to surveillance and no surveillance would reduce the potential for confounding assuming that randomization is successful. In addition, adjustment for lead and length time biases is recommended regardless of randomized or non-randomized study design.

I would like to acknowledge Rohit P. Ojha, Gilles Vassal, and Henrik Hasle for their contributions to this comment.

On 2016 Nov 05, Peter H. Asdahl commented:

I read with interest the study by Villani et al., who reported findings of a cancer surveillance program among TP53 mutation carriers. The authors analysed data from 89 TP53 mutation carriers diagnosed and followed at three tertiary cancer care centres in North America. Villani et al. concluded that their surveillance program is feasible, detects early tumour stages, and confers a sustained survival benefit. I emphasize a more conservative interpretation of the results because of biases common to observational studies of screening effects.

The primary outcome of the study was incident cancers. If the surveillance and non-surveillance groups were exchangeable at baseline (i.e. had similar distribution of known and unknown factors that affect cancer incidence), we would expect either higher frequency or earlier detection of cancer in the surveillance group because of differential detection attributable to systematic cancer surveillance. The results reported by Villani et al. are counterintuitive: 49% and 88% of individuals in the surveillance and non-surveillance groups, respectively, were diagnosed with at least one incident cancer (crude risk ratio for the effect of surveillance=0.56, 95% confidence limits: 0.41, 0.76. – n.b. risk time distribution is not included in the manuscript). This inverse result suggests that the groups were not exchangeable, and thus confounding is a concern. The potential for confounding is further supported by baseline imbalances in age, sex, and previous cancer diagnosis, which favour higher cancer incidence in the non-surveillance group (the P-values in Table 1 are misleading because of low power to detect differences).

The baseline imbalance between groups is exacerbated by lead time and length time biases when comparing survival. Detection of asymptomatic tumours by surveillance invariably adds survival time to the surveillance group and gives a spurious indication of improved survival. (Croswell JM, 2010) The effects of this bias are well-documented, and depending on the time from detection to symptom onset, the bias may be substantial. The survival analysis is further invalidated by the inclusion of non-cancerous lesions (e.g. fibroadenoma and osteochondroma, which are unlikely to affect survival) and pre-cancerous lesions (e.g. colonic adenoma and dysplastic naevus). Such lesions accounted for 40% and 16% of the incident neoplasms in the surveillance group and non-surveillance group, respectively.

Annual MRI was included in the surveillance protocol. Many of the malignancies among TP53 mutation carriers are rapidly growing, and thus more often detected by symptoms rather than annual follow-up. For example, most medulloblastoma recurrences are detected by symptoms a median of four months after the last imaging. (Torres CF, 1994)

In summary, the study by Villani et al. is not immune to biases common to observational studies of screening effects (Croswell JM, 2010) and the results should not be interpreted as a benefit of surveillance of TP53 mutation carriers as it uncritically has been done by many, which is well described in the accompanying editorial. The benefit, if any, of the proposed surveillance program cannot be assessed without a more rigorous study design to reduce known biases. For example, a study based on random allocation of individuals to surveillance and no surveillance would reduce the potential for confounding assuming that randomization is successful. In addition, adjustment for lead and length time biases is recommended regardless of randomized or non-randomized study design.

I would like to acknowledge Rohit P. Ojha, Gilles Vassal, and Henrik Hasle for their contributions to this comment.