Taufiq

He began with information theory and earned a doctorate at a leading UK university. Information theory studies how information can be measured, transmitted, and recovered under constraints. Afterwards, he taught and researched at different institutions, while gradually taking on wider responsibilities.

He described moving into new research areas, leading initiatives, and winning funding. Moreover, he told me about an upcoming appointment as a university research vice-president. The person holding that role was approaching retirement.

What impressed me most was how quickly he understood new concepts and mathematically demanding papers. He kept thinking, stayed sharp, and still made room for life outside work. I want to learn the habits behind that combination.

Therefore, I read his advice as a path towards useful responsibility. First, become good enough at something that others can rely on my judgement. Then widen what I can contribute.

He encouraged me to pursue fundamental research, which seeks explanations and principles behind particular results. His reason was the range of problems those ideas might eventually help solve. A good explanation can remain useful when the application changes.

For example, information theory asks what can be communicated reliably through noise. Different applications can share that question, even when their devices and data differ. This is how I understand the value of a foundation.

Moreover, he warned me against building my early identity around a narrow applied problem. A once-promising application may become crowded, routine, or less useful. Therefore, I want skills and questions that give me room to adapt.

However, calling a field “evergreen” cannot guarantee its future. Fundamental questions also change, and specialised knowledge can become less useful. My test is whether I am learning principles I can examine and adapt elsewhere.

The European Research Council supports research whose questions researchers propose themselves. That provides an institutional example of making room for uncertain, exploratory work. It does not settle which research direction I should choose. [1]

He used Niels Bohr, Louis Pasteur, and Thomas Alva Edison to explain different research directions. His advice was to begin near Pasteur, with some room towards Bohr. Later, I could bring that foundation into work closer to Edison.

Donald Stokes’s Pasteur’s Quadrant gives this comparison a useful structure. It separates the pursuit of fundamental understanding from attention to practical use. Therefore, a project can pursue both at once. [2]

The National Academies also explain that practical goals can inspire advances in fundamental understanding. Applied work and fundamental inquiry can feed each other. [3]

Therefore, I want a PhD where a useful problem opens a deeper question. His advice concerns my early training and the researcher I want to become. An established researcher may later emphasise delivery, while still drawing on that earlier foundation.

He recommended becoming a specialist before trying to be a generalist. Depth gives people a reason to take my contribution seriously. Moreover, working through one field teaches me how to evaluate a claim and recognise a weak explanation.

Then I can become T-shaped, with depth in one area and breadth for working with others. The vertical part represents a field I know well. The horizontal part represents enough shared understanding to collaborate across fields.

The National Academies describe combining disciplinary depth with broader interests and skills. Their recommendations include building a foundation in one discipline, then adding others as needed. They also encourage early interdisciplinary experiences. Therefore, depth and early contact with other fields can develop together. [4]

However, skill in one subject does not make me an expert in every subject. When I branch out, I must learn the new field’s evidence and limits. I can contribute a perspective while asking its specialists to correct my assumptions.

The Indonesian saying “tong kosong nyaring bunyinya” has a natural English equivalent, “empty vessels make the most noise”. I took his lesson to mean that responsibility should rest on work people can examine. Then my claims about what I can do have something behind them.

He encouraged me to pursue blue-skies research during my PhD. This means exploring questions whose answers and eventual uses are still uncertain. He wanted me to have room to investigate and develop my own judgement.

Moreover, he warned against a PhD so tightly tied to project delivery that it feels like industrial work. I understand that concern as a question about intellectual freedom. If the deliverable determines every step, where do I learn to choose a research direction?

However, a funded project can still contain a strong fundamental question. I need to examine the actual freedom, supervision, and expectations within it. The project label alone tells me little about that experience.

He stressed judgement and research taste. I understand research taste as choosing questions that deserve attention, given what matters and what I can learn. It also includes knowing which promising-looking directions to leave alone.

Therefore, I need to ask more than whether I can make a method work. What changes if I answer the question? Which assumption does it test? Who would learn something from either outcome?

The US National Science Foundation describes transformative research as work that changes understanding or opens new research directions. That gives “transformative” a more demanding meaning than a large improvement on one benchmark. Moreover, the agency says there is no formula that guarantees such research. [5]

He also taught me about selling and framing research. Each community has its own language, priorities, and standards of evidence. Therefore, I need to explain my contribution in terms its members can evaluate.

In his advice, entering a new field did not require abandoning what I already knew. I could bring a different perspective and a useful method. At the same time, I needed to learn what the community already understood.

The National Academies note that interdisciplinary collaboration takes time to learn other methods, languages, and cultures. That supports the need to learn how a community frames its problems. [4]

I want to explain my contribution clearly while giving others room to challenge it. Selling an idea means making its purpose, evidence, and costs understandable. Framing means choosing the explanation that connects those facts to the listener’s concern.

For example, I might explain how a communication limit helps examine a sensing problem. Then I would ask which conditions make that comparison valid. This is a possible introduction, rather than a claim that every problem fits my method.

His advice included understanding the politics of an institution while remaining likeable and trusted. I read that as learning how people make decisions and what they need. Good work still needs support, resources, and people willing to work together.

The Center for Creative Leadership describes political skill through social awareness, influence, relationships, and sincerity. It also recommends thinking before speaking and maintaining relationships beyond senior management. [6]

Therefore, I want to understand the setting before asking others to back an initiative. Who has authority? Who will carry the work? Who bears the risk if I am wrong?

Moreover, being pleasant to work with must leave room for disagreement. I can listen carefully, make a clear case, and change my mind when evidence warrants it. I also need to refuse commitments I cannot honestly fulfil.

Research depth can help me contribute to a decision. However, leading people also requires learning how to listen, delegate, and resolve competing needs. I want responsibility to grow alongside those skills.

The lesson I took was how research, initiative, and leadership can support each other. He described winning funding while continuing to pursue work he loved. Moreover, he connected that path with still having a life outside the role.

Therefore, I want to think about what a grant makes possible. Which question can the team now investigate? Which people, equipment, and time does it support? What obligations will it create?

DARPA’s Heilmeier questions ask researchers to explain their aims, novelty, beneficiaries, risks, costs, and tests. They offer a practical way to make a proposed project understandable. [7]

I remain impressed by how quickly he learnt a new concept or a mathematically heavy paper. His example made continued learning feel compatible with wider responsibility. Moreover, he kept returning to thinking itself as something worth maintaining.

I cannot know his whole learning method from one conversation. However, I can practise a reading habit that fits the lesson. S. Keshav’s paper-reading guide moves through orientation, closer examination, and reconstruction of the argument. [8]

For a mathematical paper, I would add a small worked example and explain one derivation without looking. Afterwards, I would compare that explanation with the paper and repair the missing steps. These are my practice choices, rather than a report of his routine.

Finally, I want the life beyond research that he spoke about. That means protecting time for relationships, rest, and interests outside the university. As responsibilities grow, I will need to decide what to delegate and which opportunities to decline.

I want this conversation to change how I choose and work. Therefore, I return to these questions when considering a PhD, project, collaboration, or leadership role.

These public stories resemble parts of the path he described. However, each person faced different opportunities, collaborators, and institutions. I use their accounts to examine choices, rather than predict a career.