A short guide to technology development in cell biology

Development of a new technique can take one to five years of full-time effort, and hence can be a risky endeavor for a young scientist. The decision to start such a project therefore requires careful weighing of the pros and cons (see text box). In essence, there are four main considerations.

First, conduct a thorough literature survey to ensure that the method has not been developed by others already, and to search for indications that the method may or may not work. The second consideration is the potential impact of the new technology. Impact is often difficult to predict, but it is linked to how broadly applicable the technology will be. Will the new technology only provide an answer to your specific biological question, or will it be more widely applicable? It may be helpful to ask: how many other scientists will be interested in using the technology, or at least will profit substantially from the resulting biological data or knowledge? If the answer is “about five,” then the impact will likely be low; if the answer is “possibly hundreds,” then it will certainly be worth the investment. This potential impact must be balanced against the third consideration, which is the estimated amount of time and effort it takes to develop the technology. The fourth major consideration is: What is the chance that my technique will actually work and what is the risk of failure? There is no general answer to this question, but below I will outline strategies to reduce the risk of failure and minimize the associated loss of time and effort. For this I will consider the common phases of technology development (Fig. 1).

An adage that is often heard in the biotechnology industry is “fail fast.” It is OK if a project turns out to be unsuccessful, as long as the failure becomes obvious soon after the start. This way the lost investment will be minimal. In an academic setting, it may also be good to prevent finding yourself empty-handed after years of work. As a rule of thumb, I suggest that one should aim to obtain a basic proof-of-principle within approximately four months of full-time work. If after this period there still is no indication that the method may eventually work, then it may be wise to terminate the project, because further efforts are then also likely to be too time-consuming. It is thus advisable to schedule a “continue/terminate” decision point about four months after the start of the project—and stick to it. Note that at this stage the proof-of-principle evidence may be rudimentary, but it is crucial that it is convincing enough to be a firm basis for the next step: optimization.

Obtaining the first proof-of-principle evidence is a reason to celebrate, but usually it is still a long way toward a robust, generally applicable method. Careful optimization is required, through iterations of systematic tuning of parameters and testing of the performance. This can be the most time-consuming phase of technology development. To keep the cycle time of the iterative optimizations short, it is essential that a quick, easy readout is chosen. This readout should be based on a simple assay that ideally requires no more than 1–2 d. It is important that the required equipment is readily accessible; for example, if for each iteration you have to wait for several weeks to get access to an overbooked shared FACS or sequencing machine, or if you depend on the goodwill of a distant collaborator who has many other things on his mind, then the optimization process will be slow and frustrating. If your technology consists of a lengthy protocol with multiple steps, try to optimize each step individually (separated from the rest of the protocol), and include good positive and negative controls.

Remember that statistical analysis is your ally: it is a tool to distinguish probable signals from random noise and thus enables you to make rational decisions in the optimization process (did condition A really yield better results than condition B?). Assays with quantitative readouts are easier to analyze statistically and are therefore preferable.

During the optimization process it is helpful to define an endpoint that will result in “version 1.0” of the technology. Typically this is when the technology is ready to address its first interesting biological question. Once you have reached this point, it may be useful to temporarily refrain from further optimization of the technology, and focus on applying it to this biological question. This has two purposes. First, it subjects the technology to a real-life test that may expose some of its shortcomings, which then need to be addressed in further optimization cycles. Second, it may yield biological data that illustrates the usefulness of the technology, which may inspire other scientists to adopt the method. If you are based in a strictly technology-oriented laboratory, collaboration with a colleague who is an expert in the biological system at hand may expedite this phase and help to work out bugs in the methodology.

If version 1.0 performs well in this biological test, it may be time to publish the method. For senior postdocs, this may also be a good moment to start your own laboratory. A new technology is usually a perfect basis for such a step.

When, upon publication, other scientists adopt your new technology, they will often implement improvements and new applications, which makes the technology attractive to yet more scientists. This snowball effect is one of the hallmarks of a high-impact technology. An extreme example is the recently developed CRISPR–Cas9 technology (Doudna and Charpentier, 2014), for which improvements and new applications are currently reported almost on a weekly basis. What can you do to get such a snowball rolling?

First, it helps to publish the new technology in a widely read or Open Access journal, to present it at conferences, and to initiate collaborations in order to reach a broad group of potential users. Second, the threshold for others to use the new technology must be as low as possible. Thus, implementation of the technology must be simple, and users must have easy access to detailed protocols. A website with troubleshooting advice, answers to frequently asked questions, and (if applicable) software for download will also help. Depending on the complexity of the technology, it may be worth considering whether to organize hands-on training, perhaps in the form of a short course. This may seem like a big investment, but it can substantially contribute to the snowball effect.

Third, materials and software required for the technology should be readily available. Technology transfer offices of research institutes often insist on the signing of a material transfer agreement (MTA) before materials such as plasmids can be shared. But all too often this leads to a substantial administrative burden and delays of weeks or even months. Free “no-strings-attached” sharing of reagents is often the best way to promote your technology—and scientific progress in general.

Before publication of the technology, you may consider protecting the intellectual property by filing a patent application. Most academic institutes do this, but often the associated costs are high and the ultimate profits uncertain, in part because it can be difficult to enforce protection of a patented technology (how do you prove that your technology was used by someone else?). That said, some technologies or associated materials may be more effectively scaled up and disseminated through a commercial route than via purely academic channels. Specific companies may have distribution infrastructure or technical expertise that is hard to match in an academic laboratory. Founding your own company may also be a way to give the technology more leverage, as it provides access to funds not available in an academic setting. In these cases, timely filing of a patent application may be essential. Note that in certain countries one cannot apply for a patent once the technology has been publicly disclosed (e.g., at a conference).

Often different technologies for the same purpose are invented independently and more or less simultaneously. It is therefore quite likely that sooner or later an alternative technology emerges in the literature, or appears on the commercial market. This is sometimes referred to as “competing technology,” but in an academic setting this is somewhat of a misnomer, as solid science requires multiple independent methods to cross-validate results. Moreover, it is extremely rare that two independent technologies cover exactly the same spectrum of applications. For example, one technology may have a higher resolution, but the other may be superior in sensitivity. The sudden emergence of a competing technology can however have strategic consequences, and it is important to carefully define the advantages of your technology and focus on these strengths.

New technologies generally consist of a new combination of available technologies, or apply newly discovered fundamental principles. Because the pool of available knowledge and tools continues to expand, the opportunities to devise and test new methods will only improve. This is further facilitated by the increasing quality of basic methods and tools to build on. Thus, there is a bright future for technology development. With a carefully designed strategy, the risks associated with such efforts can be minimized and the overall impact maximized. In the end, it is extremely gratifying to apply a “home-grown” technology to exciting biological questions, and to see other laboratories use it.

I thank members of my laboratory and Natalie de Souza for helpful suggestions. The illustration was conceived by B. van Steensel and provided by Neil Smith (www.neilsmithillustration.co.uk).

Technology development in the B. van Steensel laboratory is currently supported by European Research Council advanced grant 293662 and the Netherlands Organisation for Scientific Research (NWO) ZonMW-TOP.

The author declares no competing financial interests.