MSc students at the Iceland School of Energy where I’ve taught often ask for suggestions about appropriate thesis topics. Sometimes we find challenges in research or industry that we stockpile and could in theory parcel out for purposes such as these. Yet instead of individual suggestions, let’s discuss an overall process to gather, winnow and select topics in a way best suited for the candidate.

This will make more sense later – thanks JLB

There are four general principles one can consider when choosing a topic that requires investment of months or years of effort, and will have a bearing on life later. These principles are:

  1. Motivation
  2. Specificity
  3. Fit
  4. Flexibility

Let’s discuss.

Motivation

Intrinsic motivation, where your effort provides you with its own rewards, yields far more effectiveness and benefits than extrinsic motivations. Since your motivation should be intrinsic, by its very nature someone else cannot tell you what this “should” be, in some tidy list format. Can you state to yourself, with clarity, why this topic is something you are motivated to pursue, in accordance with your broader personal objectives?

Now, various candidates for motivation might be things like: helping save the world or your village, making a splash entering a field as a strong setup for a career, delving into a topic of great personal interest, or other factors. The important thing is not to articulate those motivations to someone else, but to yourself – and truly believe them. If you do not have a strong motivation to pursue a specific topic, it will not channel your forces as effectively as a choice that will. This motivation should be aligned with your personal objectives.

Having said that, it isn’t always about you. Your value in the world stems from your ability to provide service to others. You can increase the value of your thesis by choosing a topic and product that can be published, or lead to other work. Ideally not one that is thrown in a dusty drawer and forgotten.

ACTION ⇒ state your personal objectives clearly in writing using the SMART format. Then ask yourself how well your choice lines up with these objectives in a  way that will motivate you. For some discussions about articulating your objectives in this format, there are resources everywhere, but here are several that might help to get started:

A Clear Summary List of SMART criteria

Dave Ramsey (video) – consider the different personal categories he suggests

Google “SMART objectives” and you will find scores of useful references. Find a structure that suits you – but they must be articulated in writing. It is difficult to respond to the question “what topic should I choose?” without knowing the objectives. It is like someone asking “what is the best move in chess?” without knowing the status of the board.

Specificity

As a new, wide-eyed student looking over the panoply of technology options in the renewable energy field, it can seem daunting to try to select any specific one where an entrant can add value. How does one step into a massive pool of so many rapidly advancing fields, already populated by so many experts?

One strategy is what we could call “specificity.” You are coming into a program at a specific time, with a specific blend of talents and interests. Combine these traits to find a topic where you are uniquely suited to add value.

Geographic Specificity: let’s say you come from a small town or region that might benefit from the application of a specific renewable energy technology. How would, say, a geothermal district heating system for that community contribute in terms of performance, costs, benefits? Can the unique terrain around that area translate to wind or hydro potential? Could you harness the native biomass resources for power, fuel, heating, cooking, etc.?

It would be more difficult for an outsider to delve into the intricacies of your area’s resources, population, loads, and constraints, compared to someone as familiar with the area as you are. Use that as a differentiator to examine some aspect of the area that could benefit from renewable energy technologies. Since engineering consultancy may be spendy for a small village or area, consider structuring your work so you can share it with the public. Perhaps it might serve as a useful launching pad for a future project.

PhD projects usually call for a more profound advancement in the body of knowledge of a field than one generally expects for a MSc project. If you can achieve the former in an MSc, well and good. But in my view, even some practical technical contribution that is not necessarily cutting edge is worthwhile, so long as it has the potential for positive societal impact, no matter the scale.

The other aspect you can draw on as a differentiator is Time Specificity. You plan to carry out your work at a specific time, when various technologies and market factors are at work as at no other time before. Perhaps residential solar-PV roofing materials for your village have been studied ten years before – but what is the techno-economic situation now? What is the current status of conventional fuels, alternative technologies available, load/demand profiles, costs, and tax incentives? By using aspects of geographic and time specificity, you increase the probability that what you are doing will be unique as well as relevant.

ACTION ⇒ write down what makes you and this time a great combination of resources to tackle this project. What keen insights or new opportunities make sense for this work now?

Fit

Unless you come up with a truly earth-shattering, novel new development in a field, it is more likely that you are looking for a fit for your project that is like a component in a tall new tower.

Up we go (LEGO)

The base of your tower is the assembled work and literature in your field to date. You need to know what the current status of that work is in order to know how your new contribution fits appropriately at the “building edge.” Then, as you finish your effort, it will be helpful to give guidance to the next builders after you in terms of where you think their next steps might be well placed.

A good thesis contains both these aspects. First, a literature review showing and acknowledging the work to date, indicating the gap or fit that is intended to be filled by the current work. Then in the conclusion, some guidance for others. Perhaps someone has left such guidance for you in their existing work. Harvest notes from papers, classroom or potential advisor discussions of challenges/research regarding current technology, “hot topics” of talks at recent conferences, and news feeds covering your industries of interest. Collect various ideas over time in the months leading up to your topic selection so you understand how your work might fit into the overall scheme.

ACTION ⇒ perform your own literature review/survey of the field you are interested in, and write down topics of interest. Scan journals or conference proceedings and look for trends. If you are interested in joining a particular research or industry group, read and become familiar with their work – perhaps there will be some clues in there that can segue naturally to a discussion with them. Be able to explain why your work is a natural fit to the growing body of knowledge, and how in the future others might take the topic to a next level.

Flexibility – The Garden of Forking Paths

Jorge Luis Borges is a favorite author, incredibly imaginative, who had a short story of this name. Imagine a thesis topic selection that was so well and narrowly defined that there were few options or alternative approaches for you to elaborate upon, if you chose. That to me might be rather boring. A narrow definition can especially be a challenge for an experiment-based thesis: you decide the project will be to “determine X,” but then later discover someone else has measured X to a higher level of accuracy that you are capable of, or you run into challenges with the experiment design and cannot finish the work. Kind of stuck.

Rather, if you were to consider a topic that had a variety of avenues that you could explore, but were not required to take all on in order to finish it satisfactorily, that might be more flexible and adaptable, in case you run into roadblocks in your original plan or you decide to delve into something of new interest. Have something that inherently has “forking paths” or potential for a “pivot.”

Perhaps your original topic was to simply evaluate the technical merits of an approach,  but you find later that someone else had covered that ground (or is currently). A topic with “forking paths” might be one with the potential to expand the work to encompass other technical, financial, economic, environmental, or social aspects. You do not have to take on more than you can handle, but the project lends itself better to tuning. You can then point out future work for others, like your advisor, or yourself as a PhD.

ACTION ⇒ write down the main objective of your work, but also identify several other “forking paths” where you or someone else might continue the work later for sustained benefit.

Summary

These seem like a reasonable compilation of questions/actions one should undertake in the months and weeks leading up to a topic selection. If you can:

  1. articulate (in writing) your personal objectives,
  2. show how specificities makes you and the topic a good match,
  3. show that your topic is a fit within your objectives and the broader good of society, based on your comprehensive understanding of the big picture,
  4. and show that your topic has flexibility and adaptability to weather unexpected changes, and with potential for growth,

Then you may be off to a solid start at things.

N.B.: the above principles can apply whether you use the word topic, or job, career, partner, or other selections important to your satisfaction and happiness. Start early and use similar tools, and you might have analogous successes in those other areas of your life.

For a related post on finding thesis advisors, refer here…